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edited with a foreword fey 
James Biyanf Conanf 

These volumes of the HARVARD CASE 
signed to help the general reader relate devel- 
opments in the natural sciences to those in the 
other fields of human activity. 

No matter what his education and intelli- 
gence, the reader without research experience 
finds himself at a loss when required to evalu- 
ate the work of scientists, not because of his 
lack of scientific knowledge but because he has 
no sound general understanding of what science 
can or cannot accomplish. These narrative his- 
tories of great experiments help fill this gap by 
supplying what Dr. Conant describes as the 
"feel" for "the tactics and strategy of science/' 

Familiarity with the cases outlined in these 
volumes can lead the reader to a better under- 
standing both of modern science and of modern 
technology. And attention paid to the kinds of 
difficulties that have arisen in the past over the 
testing of new concepts gives insight into what 
is happening in the laboratories of physics and 
chemistry today. 

Edited and with a foreword by James B. 
Conant, distinguished scientist, teacher and dip- 
lomat, these histories were first prepared for 
students in the humanities and social sciences at 
Harvard College. They are now offered to a 
wider public in the belief that a detailed knowl- 
edge of a few epoch-making advances in sci- 
ence will provide a key to a better comprehen- 
sion of the modern world. 

Cambridge 38, Massachusetts 


3 1148 00112 2506 

507,2 Clkh v.l 61-07811 


Harvard case histories in 

experimental science 













Volume 1 


Copyright, 1948, 1950, 1952, 1953, 1954, 1957 by the President 
and Fellows of Harvard College. Distributed in Great Britain by 
OXFORD UNIVERSITY PRESS, London. Library of Congress Catalog 
Card Number: 57-12843. Printed in the United States of America. 

















The Harvard Case Histories in Experimental Science were 
designed primarily for students majoring in the humanities or the social 
sciences. Such students require an understanding of science that will 
help them to relate developments in the natural sciences to those in the 
other fields of human activity. To do so demands an understanding both 
of the methods of experimental science and of the growth of scientific 
research as an organized activity of society. Experience shows that a 
man who has been a successful investigator in any field of experimental 
science approaches a problem in pure or applied science, even in an area 
in which he is quite ignorant, with a special point of view. One may 
designate this point of view "understanding science"; it is independent 
of a knowledge of the scientific facts or techniques in the new area. 
Even a highly educated and intelligent citizen without research experi- 
ence will almost always fail to grasp the essentials in a discussion that 
takes place among scientists concerned with a projected inquiry. This 
will be so not because of the layman's lack of scientific knowledge or 
his failure to comprehend the technical jargon of the scientist; it will be 
to a large degree because of his fundamental ignorance of what science 
can or cannot accomplish, and his subsequent bewilderment in the 
course of a discussion outlining a plan for a future investigation. He 
has no "feel" for what we may call "the tactics and strategy of science." 
The present two-volume publication of the series was planned in 
order to make this material available to the general reading public. A 
citizen, a businessman, a public servant, a lawyer, a teacher, or a writer, 
may be called upon at some time to evaluate the work of scientists and 
to consider the ways in which such work can be organized and financed. 
He may wish also to consider to what degree systematic investigations 
more or less analogous to those that have been successful in the physical 
sciences may be fruitful in other fields. Although the first cases are con- 
cerned almost exclusively with the physical sciences, an understanding 
of the variety of methods by which these sciences have advanced will 
provide some basis, it is hoped, from which the citizen can appraise 
proposals for research and its applications in the biological and social 



In order to appreciate the methods of the experimental sciences 
it is necessary to master a certain amount of technical subject matter 
within the fields of physics and chemistry although no one can prescribe 
the particular topics to be studied. It is quite clear that one need not 
attempt the task of surveying all physics or chemistry, nor is it necessary 
to memorize comprehensive factual information about the scientific 
basis of our modern technological civilization. If one understands the 
nature of modern science, such factual information can when needed 
be readily acquired by consulting appropriate books and articles. 

A direct study of the methods of modern science presents great diffi- 
culties. A visitor to a laboratory, unless he is himself a scientist, will 
find it almost impossible to understand the work in progress; he will 
comprehend neither the objectives nor the implications of the measure- 
ments and observations that the investigator is making. To be sure, he 
may be able to appreciate in a general way the nature of the problem 
that is under investigation; he may well realize that the questions raised 
by those who planned the experiment are of importance either for 
immediate practical reasons or as part of the general advance of science. 
But unless he himself has had considerable experience with scientific 
research, he will be baffled by what he sees or hears, for almost without 
exception research problems today are concerned with areas of science 
where there is a large accumulated background of technical informa- 
tion. To be able to follow the new work one must have studied the 
advance of the science thoroughly, which usually means mastering a 
considerable amount of mathematics as well as physics or chemistry 
or biology. 

Modern science has become so complicated that today methods of 
research cannot be studied by looking over the shoulder of the scien- 
tist at work. If one could transport a visitor, however, to a laboratory 
where significant results were being obtained at an early stage in the 
history of a particular science, the situation would be far different. For 
when a science is in its infancy, and a new field is opened by a great 
pioneer, the relevant information of the past can be summed up in a 
relatively brief compass. Indeed, if the methods of experimental science 
are being successfully applied for the first time to a problem of im- 
portance, the scientist's knowledge would not be much greater than 
that of his inquiring guest. Briefly, and in simple language, he could 
explain the new experiment. Then as from day to day results were 
obtained and further experiments planned the visitor would see unfold- 
ing before him a new field. However, such periods in the history of 
science are relatively few, and it would be a fortunate visitor indeed 


who could spend some time merely as a witness of the events. For he 
would have the pleasure of knowing not only that he had been present 
at one of the critical battles in the forward march of science, but that 
he had had a unique opportunity of learning at first hand about the 
methods of science. 


The purpose of the case histories presented in this series is to 
assist the reader in recapturing the experience of those who once par- 
ticipated in exciting events in scientific history. The study of a case 
may be to some degree the equivalent of the magical operation sug- 
gested in the preceding paragraph, namely, that of transporting an 
uninformed layman to the scene of a revolutionary advance in science. 
To be sure, usually more than one investigator or laboratory is involved 
and the period of time is at least several years; for, however significant 
a single experiment may seem in retrospect, no important step forward 
in experimental science rests solely on the record of any single investi- 
gator's observations. Rather, the interplay of ideas of several men, argu- 
ments about experiments and their interpretation between workers in 
different laboratories, often mark the decisive turn in scientific thinking. 
However, by the intensive study of the actual work of some of the great 
investigators of the past (and less in detail, the work of their contem- 
poraries), the methods then employed stand out clearly. 

Some of the cases in this series present the work of men who lived 
over three hundred years ago; others are drawn from the eighteenth 
and nineteenth centuries. But irrespective of their dates, the examples 
presented illustrate the methods of modern science. Familiarity with 
those methods will increase the ease of understanding of the work of 
scientists today; as one consequence, popular accounts of scientific 
progress can be read with more appreciation. If one is face to face with 
problems of financing or organizing research, a critical but sympathetic 
attitude toward experimental investigation is a prerequisite for an in- 
telligent examination. The occasion may arise in connection with private 
industry, the expenditure of public money, or a philanthropic enterprise 
related to medicine and public health. Almost all that a trained scientist 
has to go on when he passes judgment on the prospects of a new venture 
far removed from his own specialty is his knowledge of the methods by 
which science has progressed in his own experience. To a considerable 
degree a nonscientist may come to have a similar basis for his opinions. 
An intimate acquaintance with a relatively few historic cases should 
assist him in finding his way through the complexities of modern in- 
vestigation as he listens to those who tell him what is being proposed. 



Science I have defined as a series of concepts or conceptual 
schemes arising out of experiment and observation and leading to new 
experiments and new observations. From the experimental work and 
careful observations of nature come the scientific facts that are tied 
together by the concepts and conceptual schemes of modern science. 
The rather sudden burst of interest in the new "experimental philoso- 
phy" in the seventeenth century is historically related to a new interest 
on the part of thoughtful menjn practical matters ranging from medi- 
cine through mining to the ballistics of cannon balls. But while the 
problems were often suggested by the interest of learned men in the 
practical arts, the development of science involved something more 
than the type of experimentation by which the practical arts had been 
developing for centuries. The method of reasoning employed in mathe- 
matics (for example, in geometry), commonly called deductive reason- 
ing, had to be combined with the methods of experimentation that 
came from the practical arts before science could progress rapidly. The 
interaction of these two streams of human activity was largely respon- 
sible for the development of physics and chemistry; the focus of atten- 
tion was shifted from an immediate task of improving a machine or a 
process to a curiosity about the phenomena in question. New ideas or 
concepts began to be as important as new inventions, and their inter- 
weaving began to produce conceptual fabrics whose various threads 
gained support from one another as well as from the direct results of 
experiment and observation. 

Concepts and Conceptual Schemes. The cases presented in this series 
illustrate some of the many ways in which the new ideas (concepts) 
have arisen from observation and experiment and the consequences they 
have entailed. In more than one case we shall see a new conceptual 
scheme (theory) replacing an older one, or two rival schemes in con- 
flict. The transition to a new theory is seldom easy; old ideas are apt to 
be tenacious. Looking back at the history of any branch of science we 
can see that a new conceptual scheme (theory) comes to be accepted 
because it is at least as satisfactory as the older one in relating all the 
known facts in a simple way and because it proves to be more fruitful 
of new experiments. The latter outcome is clearly a matter for the 
future, so that there can be no way to determine in advance whether a 
new concept or conceptual scheme will prove acceptable in this double 
sense; nor can one foretell how soon the next major advance will occur. 
A study of these cases makes it clear that there is no such thing as the 
scientific method, that there is no single type of conceptual scheme and 
no set of rules specifying how the next advance will be made through 


the jungle of facts that are presented by the practical arts on the one 
hand and by the experimentation and observation of scientists on the 

Speculative Ideas and Broad Wording Hypotheses. The relation 
between a speculative idea and a broad working hypothesis that be- 
comes a wide conceptual scheme is of interest. A good example is fur- 
nished by the history of the atomic theory. The notion that there are 
fundamental units ultimate particles of which matter is composed 
goes back to ancient times. But expressed merely in general terms this 
is a speculative idea until it forms the basis of a broad working hypoth- 
esis from which consequences can be deduced that are capable of experi- 
mental test. This particular speculative idea became in Dalton's hands 
a broad working hypothesis and came to be a new conceptual scheme 
only after he had shown, about 1800, how fruitful it was in connection 
with the quantitative chemical experimentation that had been initiated 
by the chemical revolution. 

Dalton's atomic theory is an instance where we can trace the origin 
of a conceptual scheme; in other cases we are uncertain how the idea 
came to the proponent's mind. Thus Torricelli seems to have been the 
first to suggest that we live in a "sea of air" that exerts a pressure 
analogous in many ways to the pressure of water on submerged objects; 
yet we have insufficient knowledge to say what led him to this idea. 
His famous experiment with a column of mercury, in which he made 
the first barometer, may have been the point of departure or it may 
have been a case of testing a deduction from a broad working hypothe- 
sis, arrived at by means that history does not record. At all events, from 
that time on a number of deduced consequences led to experiments 
nearly all of which were consistent with the ideas of Torricelli, and 
his hypothesis quickly attained the status of a new conceptual scheme. 

The cases presented in this series emphasize the prime importance of 
a broad working hypothesis that eventually becomes a new conceptual 
scheme. They illustrate the variety of mental processes by which the 
pioneers of science developed their new ideas. But it must be emphasized 
that great working hypotheses .have in the past often originated in the 
minds of these scientific pioneers as a result of mental processes that 
can best be described by such words as "inspired guess," "intuitive 
hunch," or "brilliant flash of imagination." The origins of the working 
hypotheses are to be found almost without exception in previous specu- 
lative ideas or in the previously known observations or experimental 
results. Only rarely, however, do these broad working hypotheses seem 
to have been the product of a careful examination of all the facts and a 
logical analysis of various ways of formulating a new principle. 


The Testing of Deductions from Conceptual Schemes. When first 
put forward, a new conceptual scheme may be no more than a working 
hypothesis on a grand scale. From it we can deduce, however, many 
consequences, each of which can be tested by experiment. If these tests 
confirm the deductions in a number of instances, the accumulating evi- 
dence tends to confirm the broad working hypothesis and the hypothe- 
sis may soon come to be accepted as a new conceptual scheme; its sub- 
sequent life may be short or long, for from it new consequences are 
constantly being deduced that can be verified or not by experimental 

While the modes of formulating broad working hypotheses are so 
varied as to defy generalization, the procedures by which these hypothe- 
ses are tested conform to a fairly consistent pattern. One is tempted, 
therefore, to represent the process of testing a broad conceptual scheme 
by a diagram. Unfortunately, however, the interrelations are so complex 
as to make a diagram more confusing than helpful. While our purpose 
would be defeated in the distortion necessary to compress a case history 
into a single diagram, we can perhaps suggest by a particular example, 
drawn from fart of one case, the type of process involved in the experi- 
mental testing of broad conceptual schemes. Thus, at one stage in the 
development of pneumatics, Pascal deduced from Torricelli's idea of a 
sea of air the consequence that the air pressure should be less on a 
mountain top than at the base. This deduction could be expressed in 
some such words as these: if the Torricellian experiment is performed 
at such and such a place the height of the mercury column will be 
greater than on the same day at a nearby spot high up on a mountain. 
This prediction is susceptible of a test which yields a yes or no answer. 

As the cases illustrate, however, there are often many slips in the 
argument at this point; unconscious assumptions are often involved 
that turn out to have been unwarranted. In general, the complete pat^ 
tern of deduction linking the broad working hypotheses to the experi-, 
mental tests proves far from simple. Thus, in the example just cited, 
the tacit assumption is clearly being made that the laws of liquid pres- 
sure and the density of mercury (and probably several other such 
things as well) are not themselves appreciably different at different 
altitudes; these assumptions find their ultimate justification (for the 
purposes of this experiment, at least) in other broad conceptual schemes 
such as make up the laws of hydrostatics. It is the multiplicity, the 
complexity, and indeed often the vagueness of this sort of interconnec- 
tion that is ignored in many oversimplified discussions of "the scientific 

Experimentation. The experiments performed to test deductions from 


broad working hypotheses involve in the last analysis a type of activity 
with which everyone is familiar. Examples of experimentation in every- 
day life come readily to mind. Whenever one has a choice of alternative 
ways of trying to solve a problem, decides on one, and then says in 
essence "let's try it and see," he is getting ready to perform an experi- 
ment. Framing various possibilities as to what is wrong with an auto- 
mobile engine when the car is stalled is usually a preliminary to carry- 
ing out an actual trial, an experiment. Similarly, if a man is trying to 
locate a broken wire, a blown-out fuse, or a bad tube in a radio set, he 
usually turns over in his mind a number of tests that could be made 
and then tries first one and then another. He is guided in the formula- 
tion of his trials (experiments) by his knowledge of the automobile or 
the radio set in question and his general information about the behavior 
of these machines. When he finally carries out the experiment he is, 
however, testing the validity of a very limited wording hypothesis. 
A simple and perhaps trivial example of the testing of a limited work- 
ing hypothesis is when a person trying to unlock a door puts in the lock 
a hitherto untried key and says to himself, "if this key fits the lock, then 
the lock will spring when I turn the key." The trial either validates or 
negates the limited working hypothesis; the same is true of the final 
step in most experiments in science. 

The difference between experimentation in everyday life and experi- 
mentation in science lies primarily in the fact that in the one case 
common-sense assumptions and practical experience determine the 
nature of the experiment; in the other, a series of connecting links usu- 
ally relates some deductions of a broad working hypothesis with the 
final limited working hypothesis involved in the specific experiment. 
This will be more evident as one studies the cases. The steps by which 
practical men throughout the ages have improved the practical arts 
have also involved experimentation. Here, as in everyday life, however, 
the experiment is in almost every case planned in terms of common- 
sense assumptions and practical experience, not in terms of broad 
generalizations or conceptual schemes. Furthermore, as was pointed 
out in the opening paragraph of this section, experimentation in the 
practical arts always has a practical objective. Experimental science was 
the consequence of the combination of the ancient art of experimenta- 
tion with the type of thinking that employs general ideas and deductive 
reasoning. Experimentation by itself does not produce science, although 
it is an essential element in advance in many fields of science. 

The progress of science in many areas has depended on the overcom- 
ing of experimental difficulties, in part by the invention of new instru- 
ments and the discovery of new materials. A study of the types of 


difficulties that' have arisen in the past and how they have interfered 
with the testing of new concepts and conceptual schemes throws light 
on what is going on in the laboratories of physics and chemistry today. 
Furthermore, in formulating problems according to certain conceptual 
schemes, and particularly in planning the experimental tests, it became 
necessary as science advanced to make precise and accurate many vague 
common-sense ideas, notably those connected with measurement. Old 
ideas were clarified or new ones introduced. These are the new concepts 
that are often quite as important as the broad conceptual schemes; for 
example, pressure, acceleration, mass, temperature, atom, are words that 
have now precise scientific meanings. At the time the new ideas were 
advanced that are considered in the case histories from the seventeenth, 
eighteenth, and nineteenth centuries, they were as ncvel as are in our 
own times the ideas of neutrinos and mesons in the field of nuclear 

A close attention to the difficulties that have beset investigators in 
getting clean-cut answers to apparently simple questions will suggest 
some of the complexities of research today. And the broader hypotheses 
must remain speculative ideas until one can by the processes indicated 
succeed in relating them to experiments. 


The relation between advances in the practical arts (such as 
mining, agriculture, manufacturing) and progress in science is more 
complicated than at first sight appears. To appreciate the present situa- 
tion, it is helpful to have some knowledge of the history of these two 
branches of human endeavor and of their interaction. For many gen- 
erations after the new experimental philosophy was put forward by a 
few amateurs in the seventeenth century, the direct impact of science 
on the practical arts was almost negligible. This was the consequence 
not of any lack of interest in practical affairs on the part of the early 
scientists but of the fragmentary nature of the knowledge they acquired 
and the inadequacy of the conceptual schemes they elaborated. The 
advances in the practical arts of mining, metal making, agriculture, 
food processing, and medicine in the eighteenth and early nineteenth 
centuries were made without any very direct benefit of science. (The art 
of navigation is an exception to this statement.) 

The ancient method of experiment, the use of the "let's-try-it-and-see" 
type of reasoning in solving immediate practical problems, has led over 
the centuries to amazing results. This process of advance is often called 
pure empiricism, there being no wide generalization to guide the in- 
ventor. Even today in the mid-twentieth century when science has 


penetrated so deeply into industry, there is still a great deal of empiri- 
cism in a practical art such as steel making. Even when no practical aim 
is involved, the practical methods of a science may contain many recipes 
and rules that have no relation to theory; in other words, there is some 
empiricism in almost all scientific procedures even now. It is often con- 
venient to speak of the "degree of empiricism" in a given industrial 
process or branch of science. Where wide generalizations and theory 
enable one to calculate in advance the results of an experiment or to de- 
sign a machine (a microscope or a telescope, for example), we may say 
that the degree of empiricism is low or that the theoretical component 
of the knowledge is large. On the other hand, if the conditions for satis- 
factory operation of a machine, a process, or an instrument are based 
only on cut-and-try experimentation (as is true in some branches of 
chemistry), we may say that the degree of empiricism in that branch 
of science is still high or that the theoretical component is small. 


Applied research may be defined as research directed to the 
end of reducing the degree of empiricism or increasing the theoretical 
component in a practical art. Activities concerned solely with developing 
and improving our conceptual schemes and filling in gaps in our sys- 
tematic knowledge may be defined as pure science. Modern science is a 
fabric the texture of which is composed of many interrelated concepts 
and conceptual schemes. Today the validity of each conceptual scheme 
must be tested in the light of our total knowledge. The cases presented in 
this series fall in the category of pure science; they are nevertheless con- 
cerned for the most part with episodes in the history of science that 
eventually had great influence on applied science. The conceptual 
schemes elaborated by scientists have been fundamental to further dis- 
coveries and to the formulation of the ideas that are the fabric of modern 
science. With the aid of the concepts and theories developed over the 
past three hundred years, and drawing on the sytematic knowledge accu- , 
rnulated during that period, the applied scientist today can improve the 
industrial arts and invent new processes, products, and machines far 
more readily than could his predecessors of the seventeenth and 
eighteenth centuries. Science today is closely connected with technology 
because theory and the practical arts have become closely interwoven. 
The degree of empiricism has been lowered on almost every hand and is 
being still further reduced by the activity of investigators in laboratories 
of both pure and applied science. The applied scientist or engineer can 
now engage in what was once an activity of those inventors who pro- 
ceeded largely empirically. The analysis of experimental science pre- 


sented in this introduction and a study of the cases outlined in this series 
may lead the layman to a better understanding both of modern science 
and of modem technology. It was with this hope in mind that the 
present edition has been prepared. If the reader is stimulated to read 
further in the history of science and to follow current developments in 
some field through articles and books prepared for the general reader, 
our aim will have been achieved. 

New YorJ( City 
August i, 1957 


Robert Boyle's 
Experiments in 






If, in the last quarter of the seventeenth century, a well-edu- 
cated person in England or France had been asked why water rises in 
a suction pump, the answer would have been in terms familiar to our 
ears. Phrases such as "pressure of the atmosphere/' "creation of a 
vacuum," "air pressure dependent on the height above sea level" would 
have been used 250 years ago much as we use them in our own time. 
But if we jump back in our imagination a little more than three cen- 
turies, say to 1620, the picture changes. We have clear evidence from 
the printed records of those days that no such explanation of the action 
of suction pumps was available even to the most learned and clear- 
headed men of that time. People were talking in terms of "nature's 
abhorring a vacuum" and were unable to account for the fact that at 
sea level a suction pump will not raise water more than about 34 feet. 

The radical change that took place between the first and last quarters 
of the seventeenth century was not confined to discussions of the action 
of pumps. During the fifty years in question there was a rapid develop- 
ment of what we now call science and was then known as "experimental 
philosophy." This changed attitude and the process by which the new 
knowledge was obtained are very well illustrated by a study of seven- 
teenth-century experiments with air and the effect of air pressure on 
liquids. This subject was called in those days pneumatics. By tracing the 
growth of the new ideas (concepts) by which ever since that time people 
have explained a variety of phenomena, we obtain a "case history" of the 
way in which the experimental sciences developed* 

For convenience, the study of pneumatics between 1630 and 1680 may 
be thought of in terms of the following subdivisions: 

(i) Torricelli's experiment with a column of mercury, which included 
the invention of the barometer and his formulation of the conceptual 
scheme of a "sea of air" surrounding the e? r th; 

(ii) Pascal's repetition of the Torricellian experiment and his instiga- 
tion of the measurement of the barometric height at the foot and on 
the top of a mountain, In 1648; 

4 CASE 1 

(iii) Experiments with pumps to produce a vacuum, by von Guericke 
and by Boyle, 1650-1660; 

(iv) Examination by Boyle of the phenomena accessible for study by 
means o a vacuum pump, including the search for a "more subtle 
fluid'' than air, 1660-1680; 

(v) A study o the compressibility of air as compared with that of 
water, including the discovery of Boyle's Law, 1660-1680. 

Evangelista Torricelli (1608-1647), an Italian mathematician, was 
strongly influenced by the writings on mechanics of the Italian physicist 
Galileo. He worked on projectile motion and hydrodynamics, but is 
probably best known for the experiment that bears his name. 

Blaise Pascal (1623-1662) is at least as well known for his philosophic 
writings and his work in mathematics as for his contributions to pneu- 
matics. A mathematical theorem that bears his name was published 
when he was sixteen, and by the age of 31 he had assisted in establish- 
ing the mathematical theory of probability. He renounced scientific 
activity shortly thereafter, and during the last eight years of his life he 
was associated with the religious group known as the Jansenists. 

Otto von Guericke (1602-1686), mayor of Magdeburg and a military 
engineer, performed many experiments similar to those of Boyle, and 
at about the same time. He built a water barometer some three stories 
high, and observed the variations of the height of the water from day 

to day. 

Robert Boyle (1627-1691) is the central figure in this case. The 
seventh and last son of the "great" Earl of Cork, Boyle was a man of 
wealth who devoted his life to religion and science. Too young to have 
taken part in the Civil War in England in the middle of the seventeenth 
century, he resided in Oxford at the time when the Puritan element 
was in the ascendancy in the University. It was the gathering of amateur 
scientists in Oxford in the 1650*5 that led to the formation of the Royal 
Society in 1660, after the Restoration. 

In Section 6 we shall consider briefly the relation of science to the 
practical arts in the seventeenth century. We shall see that the interest 
in pneumatics was connected to some degree with a concern of learned 
men with the performance of the common suction pump for raising 
water. The fact that water would not rise above a certain height in such 
a pump was almost certainly known to Torricelli, and it may well be 
that pondering on this phenomenon led him directly to his experiment 
with a liquid about 14 times as heavy as water, namely, liquid mercury. 
From this line of thinking may have developed the idea that a column 
of mercury only about %4 as high as the column of water could be 
supported by atmospheric pressure. Quite apart from the new interest 
in technologic matters, interest in pneumatics was also probably in- 


creased by the publication in 1575 of a Latin translation of an Alexan- 
drian writer, Hero, on this subject. This new edition of an ancient 
treatise -was well known by the beginning of the seventeenth century 
and called to peoples' minds many phenomena, including the action of 
a siphon and the fact that a liquid cannot flow from a closed vessel 
unless air can get in. 

We can start our Case by considering the performance of the follow- 
ing experiment by Torricelli in 1643. Taking a glass tube (see Fig. i) 

FIG. i. Torricelli's experiment with a column of mercury in a tube longer 
than 30 inches. 

somewhat less than an inch in diameter and about a yard long, with 
one end closed, he filled the tube with mercury. Then, placing a finger 
over the open upper end, he inverted the tube so that the open end was 
immersed in an open dish of mercury. When he removed his finger 
from the open end, the mercury in the tube fell until the top of the 
mercury column was about 30 inches above the level of the mercury in 
the open dish. Between the top of the mercury column and the upper 
end of the tube was an empty space, which became known as a Torri- 
cellian vacuum. We shall see Boyle referring to this experiment as the 
experiment of Torricellius, or as the experiment de vacuo} 

1 A group in Florence, members of a scientific society called the Accademia del 
Cimento (Academy of Experiment), continued experiments with vacuum after 
Torricelli's death. They soon contrived to have the top of the tube consist of a 

6 CASE 1 

What led Torrlcelli to perform this famous experiment we cannot say. 
It may have been an accidental discovery, the consequence of an interest 
in the flow of liquids from small orifices; we know that Torricelli had 
been experimenting in this field. But more probably it was the act of 
an investigator who wished to test a deduction from a new idea a 
working hypothesis on a grand scale. For in the earliest account 2 of the 
experiment that we have in Torricelli's own words, there is clearly set 
forth the new conceptual scheme. What most of us today regard as a 
fact, namely, that the earth is surrounded by a sea of air that exerts 
pressure, was in the 1640'$ a new conceptual scheme that had still to 
weather a series of experimental tests before it would be generally 

Torricelli would never have been able to formulate his ideas as 
clearly as he did, however, if it had not been for earlier work of those 
who were concerned with the pressure of liquids. The subject is known 
as hydrostatics and the enunciation of the general principles involved 
goes back as far as Archimedes (B.C. 287? -2 12). Thanks to clear-headed 
writers in the sixteenth century, and in particular to Simon Stevin of 
Bruges (1548-1620), Torricelli and many of his contemporaries were 
familiar with such concepts as "pressure," which is force per unit area 
of surface, and "equilibrium." They knew that the pressure on the bottom 
of a vessel filled with a liquid depended on the height of the liquid in 
the vessel but not on its volume or its shape [Fig. 2(a)]. They realized 
that if the stopcock joining two vessels, one containing water, the other 
empty of water and open to the air, is quickly opened, the water will 
flow from one to the other, and soon the heights of the liquid will be 
the same [Fig. 2(b)}\ the system is then in equilibrium. But for a few 
seconds before equilibrium is reached, the liquid may surge back and 
forth a little. The principles relating pressure and height of liquid were 
applicable only in the equilibrium state. 

bulb in which various devices could be placed. The whole could then be filled 
with mercury and inverted in the usual way, so that the device would be in a 
Torricellian vacuum. The results of these experiments were not published until 
after the publication of Boyle's first book, but he must have heard of them by 
word of mouth or by letter. We shall see that, although many of the experi- 
ments performed in vacua by Boyle and by von Guericke could also be per- 
formed in a Torricellian vacuum, by using a vacuum produced by an air pump 
they were able to work on a larger scale and in a less awkward way. 
*A letter from Torricelli to Cardinal Ricci, dated Florence, June n, 1644. For 
an English translation, see The Physical Treatises of Pascal^ translated by 
I. H. B. and A. G. H. Spiers (Columbia University Press, New York, 1937), 
pp. 163-170. Students of this case are strongly urged to read this exchange of 
letters between Torricelli and Ricci. 


Armed with these concepts of hydrostatics, Torricelli and, after him, 
Pascal could formulate ideas about a sea of air. They could easily answer 


^=7 h' 


FIG. 2. Diagrams to illustrate the principles of hydrostatics known to Torricelli 
and his contemporaries: (a) in a homogeneous body of liquid, the pressure (force 
per unit area) at a given point depends on the depth below the surface; if the 
liquids in A and B are the same and homogeneous, the pressures at A f and B r 
are the same if h = A'; (b) in equilibrium, the levels of the liquids in connecting 
vessels are the same whatever the shapes of the vessels. 

doubting Thomases who asked why the barometer did not fall if it 
were placed inside a large glass vessel that was sealed off from the sur- 
rounding air (Fig. 3). (This is one of the first objections on record to 
Torricellf s new idea of a sea of air. The answer was of course that the 
pressure inside the enclosing vessel was the same as the atmospheric 
pressure when the vessel was first closed off. There would be no change 
of pressure on the outer surface of the mercury of the barometer unless 
some of the air was removed. And it was precisely this that Boyle set out 
to accomplish!) 


Pascal saw that from Torricelli's new conceptual scheme one could 
draw a logical conclusion susceptible of experimental test. For if the 
mercury column in Torricelli's new instrument the barometer were 
held up by the pressure of a sea of air, this pressure should be less above 
the earth's surface than at sea level. Just as the hydrostatic pressure in 

30 inches 
at sea level 


FIG. 3. Diagram of a barometer, with the reservoir B enclosed in a vessel DEF. 
Will the mercury in tube A fall into the reservoir B if the orifice C is sealed? 

the ocean diminishes as a diver ascends from the bottom of a harbor 
toward the surface, so the pressure of the air should diminish as one 
ascends a mountain. From this line of reasoning came an experiment 
performed on the Puy-de-Dome, a mountain in central France. Trans- 
lating Pascal's deduction into specific experimental terms, one could say 
that the height ot the mercury in a Torricellian experiment performed 
high on the mountain should be considerably less than if the experiment 
were conducted at the foot. The experiment was performed in 1648 by 
Pascal's brother-in-law, Perier, 3 and the deduction was confirmed. One 
cannot help, however, but be somewhat skeptical of the high degree of 
accuracy reported by Perier. To be able to repeat the Torricellian ex- 
periment so that there was less than a twelfth of an inch (one "line") 
difference in successive readings, as Perier claimed, is remarkable. The 
accidental intrusion of a slight amount of air is very difficult to avoid. 

8 For an English translation of Perier's report, see The Physical Treatises of 
Pascal, pp. 97-120, and also preface, pp. ix-xxiv. This material can be read 
with profit by the student of this case, and is strongly recommended. 


This report of Perier's was written, it must be remembered, before 
standards of accurate reporting in science had been established. The 
contrast with Boyle's procedures is striking. It may be that Perier, per- 
suaded of the reality of the large differences in height of the mercury 
column at the top and bottom of the mountain., succumbed to the 
temptation of making his argument appear convincing by recording 
exact reproducibility of his results on repeated trials. 

Robert Boyle heard of these experiments of Perier's in the 1650*8, 
although the formal publication of Pascal's treatise dealing with hydro- 
statics and pneumatics was delayed until 1663. Boyle also knew of the 
air pump that had been constructed by Otto von Guericke and had 
heard of the Florentine method of performing experiments in a 
vacuum. (See footnote i. The first full account of these experiments 
of the members of the Accademia del Cimento, however, was not pub- 
lished until 1667; von Guericke's pump was described briefly in a book 
by K. Schott in 1657.) Boyle saw the importance of having a more 
convenient method of removing the air from a glass globe in which 
various pieces of apparatus could be placed. In particular, he was inter- 
ested in testing one of the deductions from Torricelli's conceptual 
scheme, namely, that if the air is removed from above the mercury 
reservoir of a barometer, the mercury column will fall In other words, 
he desired to have an instrument with which he could evacuate the 
vessel DEF in Fig. 3 (with C closed). 

The following sections of the Case History deal with (i) the con- 
struction of Boyle's pump; (ii) the experiment for which it was partic- 
ularly designed; (iii) certain experiments on the transmission of sound 
which illustrate some of the many experiments Boyle was able to per- 
form with his new pump; (iv) Boyle's search for a more subtle fluid; 
(v) his discovery, as a consequence of a controversy about the validity 
of his ideas, of what is now known as Boyle's law. 

Boyle's work in pneumatics is an excellent illustration of the signif- 
icance of improvement in experimental equipment for the advance of 
science. His improved pump made possible the exploration of a wide 
field of study; it was for his day the equivalent of the x-ray tubes of the 
late nineteenth century, the cyclotron of the twentieth century and per- 
haps even the experimental "piles" that since 1945 have produced radio- 
active isotopes as a consequence of the release of "atomic" energy. Boyle's 
experiments offered many instances of the care with which an experi- 
menter in a new field must operate in order to obtain significant results. 
Mechanical difficulties must be overcome and this is by no means easy; 
moreover, new instruments must be invented, such as a gauge for 
showing the pressure in an evacuated vessel. 

10 CASE 1 

A careful analysis of Boyle's reports of his experiments will bring 
out the distinction between the limited working hypothesis and its 
verification or negation on the one hand, and the broad working hy- 
potheses which, if successful, as will be seen, will soon become new 
conceptual schemes. Of the latter we note in this case four in particular : 
first, the "sea of air" hypothesis originating with Torricelli; second, the 
concept of air as an elastic fluid, or in Boyle's words, that air has a 
spring; third, that sound is transmitted by air; fourth, one that was not 
successful, namely, that there is a subtle fluid which pervades all space. 

The limited working hypotheses are as numerous as the experiments. 
When Boyle built his engine he set out to test one deduction from 
Torricelli's broad hypothesis. When he had his apparatus all arranged 
he reasoned somewhat as follows : "If I now operate the pump, then the 
mercury column in the Torricellian tube should fall." This, be it noted, 
is a hypothesis strictly limited to that particular experiment. He pro- 
ceeded with the experiment and the results were as predicted. He em- 
ployed a similar "if . . . then" type of statement when he considered 
introducing air into the receiver; the mercury rose, as predicted. The 
student will find it profitable to identify a number of similar instances 
of this use of the limited working hypothesis in the experiments on 
sound and in Boyle's search for a subtle fluid. The connection between 
these limited working hypotheses and the broader idea that is being 
tested often involves a number of assumptions, sometimes not made 
explicit by Boyle. This is particularly clear in the experiments recorded 
in Sec. 4. Boyle's experiments did not disprove the existence of a subtle 
fluid in general. They could only test the presence in the air he examined 
of a specific fluid, more subtle than air, but having certain properties. 
These properties were such as to cause an effect on the instruments he 
manipulated in a vacuum (see pp. 39-48) if the subtle fluid were present. 

The experiments that Boyle performed in his search for a subtle 
fluid may seem naive and foolish to us, but a little thought will make 
it clear that they were well conceived to test a real possibility. For all 
the seventeenth-century investigators knew, air might have been com- 
posed of two or more materials differing in their ability to pass through 
very fine holes; such a difference is taken advantage of whenever we 
strain out a finely divided solid from a liquid, for example. Indeed, we 
now know that there is a very slight difference in the rate at which the 
constituent gases of the atmosphere (chiefly oxygen and nitrogen) flow 
through a tube of very small diameter. But this difference is so slight 
that it is not reflected in any behavior of air in experiments that could 
be performed with the equipment available in the seventeenth or even 
the eighteenth century. The great difference in "subtlety" for which 
Boyle was looking does not exist in any mixture of gases. It is in the 


nature of a gas that there can be no gross nonhomogeneity in the mix- 
ture, such as occurs in a suspension of fine particles of clay in water or 
even in water solutions of the materials that are present in blood or milk. 
More than a century elapsed, however, before it became obvious that 
such was indeed the case. And it was almost two centuries before the con- 
ceptual scheme was developed which we now use in all our explanations 
of the behavior of air and other gases (the kinetic theory of gases). 

In reading the original records of the seventeenth-century investiga- 
tors, the student will wish to have firmly in mind the simple ideas about 
atmospheric pressure that are almost common knowledge today. There 
are one or two less obvious points that now seem clear to us but long 
were puzzles to those who studied pneumatics in the seventeenth and 
eighteenth centuries. The first / concerns the presence of water vapor in 
the atmosphere; the second," the evaporation of liquids both below the 
temperature at which they boil and during the process of boiling itself. 
Since the first notions that developed about the evaporation of water 
into the atmosphere were either wrong or confused, we are omitting 
the seventeenth-century experiments dealing with this subject. 

At first Boyle was confused by the fact that water contains dissolved 
air, but he eventually came to understand the relation between boiling 
point and the pressure of the surrounding atmosphere; indeed, he in- 
vented an apparatus for distilling in vacua. The question of the chemical 
homogeneity of the atmosphere had to be explored before a satisfactory 
picture could be developed and the relation of liquid water to water 
vapor properly understood. This hiatus must be mentioned, for today 
every reader of the weather reports is familiar not only with variations in 
atmospheric pressure but also with the degree of humidity on a given 
day. For a long time little or no sense could be made of the fluctuations 
in the barometer because it was believed that these fluctuations were 
directly related to what we now call humidity (that is, the relative 
amount of water vapor in the air) . The student will naturally wonder 
what Boyle and his contemporaries made of their observations of the 
changes in the atmospheric pressure and of the behavior of water in 
the vacuum that they produced. Boyle and his contemporaries studied 
these phenomena but came to no satisfactory and enduring conclusions. 
This serves to illustrate the slow stages by which science often advances. 


There were three models of Boyle's "pneumatical engine," as 
he called his pump for producing a vacuum. The first, described in a 
book published in 1660 (dated December 20, 1659), is shown in Figs. 

12 CASE 1 

4 and 5; a second is described in another book dated March 24, 1667 
and published in 1669; and a third was described in a volume published 
in 1680. In the construction o the first two o these engines Robert 
Hooke played an important and perhaps determining role; the third 
was designed by Denis Papin in 1676 and was brought with him from 
France in the same year that he joined Boyle. As compared with the 
first air pump of von Guericke, Boyle's first model was far more con- 
venient for those who wished to perform experiments in vacuo. The 
opening at the top o the glass bulb was the important new addition. 
The second model of Boyle's engine (Fig. 7) allowed various types of 
receivers to be evacuated, such as those shown in Fig. 8. Much larger 
equipment could be placed in vacuo than with the first model. The ex- 
periments were correspondingly more ambitious. The third model was 
more rapid in its action because it had two plungers and two pistons 
and was operated by foot power. The valves were automatic. Boyle like- 
wise devised methods of measuring the diminished pressure by means 
of what are now called vacuum gauges; he also built compression 
pumps that enabled him to study air under pressure. 

Boyle's public announcement of the construction of his first pump 
and the description of the experiments he performed were given in his 
book of 1660, carrying the title page: 



The SPRING of the AIR, 

and its EFFECTS, 

(Made, for the most part, in a New 

Written by way of LETTER 
To the Right Honorable Charles 

Lord Vicount of Dungarvan, 
Eldest Son to the EARL of CORKE. 

The first sections of the preface are of some general interest even 
today and therefore are given below; 4 

To the Reader 

Although the following treatise being far more prolix than becomes 
a letter, and than I at first intended it, I am very unwilling to encrease 

* All quotations of Robert Boyle's writings are taken from a late edition of his 
collected writings, The Wor\s of the Honourable Robert Boyle (London, 1772), 


the already excessive bulk of the book by a preface; yet there are some 
particulars, that I think myself obliged to take notice of to the reader, 
as things that will either concern him to know, or me to have known. 

In the first place then: If it be demanded why I publish to the world 
a letter, which, by its style and divers passages, appears to have been 
written as well for, as to a particular person; I have chiefly these two 
things to answer; the one, that the experiments therein related, having 
been many of them tried in the presence of ingenious men, and by that 
means having made some noise among the Virtuosi (insomuch that 
some of them have been sent into foreign countries, where they have 
had the luck not to be despised) I could not, without quite tiring more 
than one amanuensis, give out half as many copies of them as were so 
earnestly desired, that I could not civilly refuse them. The other, that 
intelligent persons in matters of this kind persuade me, that the publi- 
cation of what I had observed touching the nature of the air, would 
not be useless to the world; and that in an age so taken with novelties 
as is ours, these new experiments would be grateful to the lovers of 
free and real learning: so that I might at once comply with my grand 
design of promoting experimental and useful philosophy, and obtain 
the great satisfaction of giving some to ingenious men; the hope of 
which is, I confess, a temptation, that I cannot easily resist. 

Of my being somewhat prolix in many of my experiments, I have 
these reasons to render: that some of them being altogether new, seemed 
to need the being circumstantially related, to keep the reader from dis- 
trusting them: that divers circumstances I did here and there set down 
for fear of forgetting them, when I may hereafter have occasion to 
make use of them in my other writings: that in divers cases I thought 
it necessary to deliver things circumstantially, that the person I addressed 
them to might, without mistake, and with as little trouble as is possible, 
be able to repeat such unusual experiments: and that after I consented 
to let my observations be made public, the most ordinary reason of my 
prolixity was, that foreseeing, that such a trouble as I met with in mak- 
ing those trials carefully, and the great expence of time that they neces- 
sarily require (not to mention the charges of making the engine, and 
employing a man to manage it) will probably keep most men from 
trying again these experiments, I thought I might do the generality of my 
readers no unacceptable piece of service, by so punctually relating what 
I carefully observed, that they may look upon these narratives as stand- 
ing records in our new pneumatics, and need not reiterate themselves an 
experiment to have as distinct an idea of it, as may suffice them to 
ground their reflexions and speculations upon. . . . 

Boyle's description of the construction of his engine is very long and 
rather tedious. A few paragraphs will illustrate the great detail with 
which he reported his work. In so doing, Boyle was setting the model 
for subsequent scientists. Unless experiments are reported in detail and 

14 CASE 1 

with accuracy, other scientists are often unable to repeat the experi- 
ment in question. The more complicated the phenomena investigated, 
the more necessary it becomes to establish the practice of recording and 
reporting details o construction of the apparatus and the results ob- 
tained. Failure to adhere to these rules in the seventeenth and eighteenth 
centuries often made worthless the reports of many investigators. The 
published works of Stevin, Galileo, and Pascal (to name the more 
important of Boyle's predecessors), are written for the most part in the 
form of geometric propositions and it is often not clear whether the 
experiments described were actually carried out or are to be regarded 
as possible demonstrations. 

The introduction of Boyle's book is in the form of a letter to his 
nephew, of which the first sections are printed below. 

Receiving in your last from Paris a desire, that I would add some 
more experiments to those I formerly sent you over; I could not be so 
much your servant as I am, without looking upon that desire as a com- 
mand; and consequently, without thinking myself obliged to consider 
by what sort of experiments it might the most acceptably be obeyed. 
And at the same time, perceiving by letters from some other ingenious 
persons at Paris, that several of the Virtuosi there were very intent upon 
the examination of the interest of the air, in hindering the descent of 
the quicksilver, in the famous experiment touching a vacuum; 1 thought 
I could not comply with your desires in a more fit and seasonable manner, 
than by prosecuting and endeavouring to promote that noble experiment 
of Torricellius [see p. 5]; and by presenting your Lordship an account 
of my attempts to illustrate a subject, about which its being so much dis- 
coursed of where you are, together with your inbred curiosity, and love 
of experimental learning, made me suppose you sufficiently inquisitive. 

And though I pretend not to acquaint you, on this occasion, with any 
store of new discoveries, yet possibly I shall be so happy, as to assist you 
to know some things, which you did formerly but suppose; and shall 
present you, if not with new theories, at least with new proofs of such 
as are not yet become unquestionable. And if what I shall deliver hath 
the good fortune to encourage and assist you to prosecute the hints it 
will afford, I shall account myself, in paying of a duty to you, to have 
done a piece of service to the commonwealth of learning. Since it may 
highly conduce to the advancement of that experimental philosophy, the 
effectual pursuit of which requires as well a purse as a brain, to endear 
it to hopeful persons of your quality, who may accomplish many things, 
which others cannot but wish, or at most but design, by being able to em- 
ploy the presents of fortune in the search of the mysteries of nature. 

And I am not faintly induced to make choice of this subject, rather 
than any of the expected chymical ones, to entertain your Lordship upon, 


by these two considerations: the one, that the air being so necessary to 
human life, that not only the generality of men, but most other creatures 
that breathe, cannot live many minutes without it, any considerable 
discovery of its nature seems likely to prove of moment to mankind. 
And the other is, that the ambient air being that, whereto both our own 
bodies, and most of the others we deal with here below, are almost per- 
petually contiguous, not only its alterations have a notable and manifest 
share in those obvious effects, that men have already been invited to 
ascribe thereunto, (such as are the various distempers incident to human 
bodies, especially if crazy in the spring, the autumn, and also on most of 
the great and sudden changes of weather;) but likewise, the further dis- 
covery of the nature of the air will probably discover to us, that it con- 
curs more or less to the exhibiting o many phenomena, in which it hath 
hitherto scarce been suspected to have any interest. So that a true account 
of any experiment that is new concerning a thing, wherewith we have 
such constant and necessary intercourse, may not only prove of some ad- 
vantage to human life, but gratify philosophers, by promoting their 
speculations on a subject, which hath so much opportunity to solicit their 
curiosity. . . . 

You may be pleased to remember, that a while before our separation 
in England, I told you of a book, that I had heard of, but not perused, 
published by the industrious Jesuit 8chottus\ wherein, it was said, he 
related how that ingenious gentleman, Otto Geric\e, consul of Magde- 
burg, had lately practised in Germany a way of emptying glass vessels, 
by sucking out the air at the mouth of the vessel, plunged under water. 
And you may also perhaps remember, that I expressed myself much de- 
lighted with this experiment, since thereby the great force of the external 
air (either rushing in at the opened orifice of the emptied vessel, or vio- 
lently forcing up the water into it) was rendered more obvious and 
conspicuous than in any experiment that I had formerly seen. And 
though it may appear by some of those writings I sometimes shewed 
your Lordship, that I had been solicitous to try things upon the same 
ground; yet in regard this gentleman was before-hand with me in produc- 
ing such considerable effects by means of the exsuction of air, I think 
myself obliged to acknowledge the assistance and encouragement the 
report of his performances hath afforded me. 

But as few inventions happen to be at first so complete, as not to be 
either blemished with some deficiencies needful to be remedied, or 
otherwise capable of improvement; so when the engine, we have been 
speaking of, comes to be more attentively considered, there will appear 
two very considerable things to be desired in it. For first, the wind- 
pump (as somebody not improperly calls it) is so contrived, that to 
evacuate the vessel, there is required the continual labour of two strong 
men for divers hours. And next (which is an imperfection of much 
greater moment) the receiver, or glass to be emptied, consisting of one 
entire and uninterrupted globe and neck of glass; the whole engine is so 
made, that things cannot be conveyed into it, whereon to try experi- 

16 CASE 1 

ments: so that there seems but little (if any thing) more to be expected 
from it, than those very few phaenomena, that have been already ob- 
served by the author, and recorded by Schottus. Wherefore to remedy 
these inconveniences, I put both Mr. G. and R. Hoo^ (who hath also 
the honour to be known to your Lordship, and was with me when I 
had these things under consideration) to contrive some air-pump, that 
might not, like the other, need to be kept under water (which on divers 
occasions is inconvenient) and might be more easily managed: and after 
an unsuccessful trial or two of ways proposed by others, the last-named 
person fitted me with a pump, anon to be described. And thus the first 
imperfection of the German engine was in good measure, though not 
perfectly remedied: and to supply the second defect, it was considered, 
that it would not perhaps prove impossible to leave in the glass to be 
emptied a hole large enough to put in a man's arm cloathed; and con- 
sequently other bodies, not bigger than it, or longer than the inside of 
the vessel. And this design seemed the more hopeful, because I remem- 
bered, that having several years before often made the experiment de 
vacua [see p. 5] with my own hands; I had, to examine some conjec- 
tures that occurred to me about it, caused glasses to be made with a hole 
at that end, which uses to be sealed up, and had nevertheless been able, 
as occasion required, to make use of such tubes, as if no such holes had 
been left in them, by devising stopples for them, made of the common 
plaister called diachylon [a sealing wax] ; which, I rightly enough guessed, 
would, by reason of the exquisite commixtion of its small parts, and close- 
ness of its texture, deny all access to the external air. Wherefore, supposing 
that by the help of such plaisters carefully laid upon the commissures 
of the stopple and hole to be made in the receiver, the external air 
might be hindered from insinuating itself between them into the vessel, 
we caused several such glasses, as you will find described a little lower, 
to be blown at the glass-house. And though we could not get the 
workmen to blow any of them so large, or of so convenient a shape as 
we would fain have had; yet finding one to be tolerably fit, and less 
unfit than any of the rest, we were content to make use of it in that 
engine; of which, I suppose, you by this time expect a description in 
order to the recital of the phenomena exhibited by it. 

To give your Lordship then, in the first place, some account of the 
engine itself; it consists of two principal parts; a glass vessel, and a 
pump to draw the air out of it [Figs. 4 and 5] . 

The former of these (which we, with the glass-men, shall often call 
a receiver, for its affinity to the large vessels of that name, used by 
chymists) consists of a glass with a wide hole at the top, of a cover to 
that hole, and of a stop-cock fastened to the end of the neck, at the 

The shape of the glass, you will find expressed in the first figure of 
the annexed scheme. And for the size of it, it contained about 30 wine 
quarts, each of them containing near two pound (of 16 ounces to the 
pound) of water. We should have been better pleased with a more 



capacious vessel; but the glass-men professed themselves unable to blow 
a larger, of such a thickness and shape as was requisite to our purpose. 

3-snch hole sealed 
by stopper 



or key 

Brass plug 

fitting hole 


Ceather washer 

Piston or 


when turned 
raises and 



FIG. 4. Diagram of the first model of Boyle's air pump. 

Cog wheel 


The seventeenth experiment reported by Boyle in his volume 
of 1660 was the critical one for which he says he built the engine. No 
one had ever put this particular consequence of the new conceptual 
scheme to the experimental test. This experiment is, therefore, typical 
of a procedure repeatedly used with great effectiveness in the advance 
of the experimental sciences. From a new concept or conceptual scheme 
one can deduce that if the concept or set of concepts is a satisfactory 
scheme, then certain deductions follow that may be susceptible of ex- 
perimental test. 

Boyle saw that a new apparatus (von Guericke's pump), if improved 
and somewhat changed, would enable him to put to the experimental 
test another consequence of the new concepts about the atmosphere 
and its pressure. This he did in the manner described in the extract 
presented below. This combination of the possibilities inherent in a 
new type of machine or a new chemical process and the necessary 
consequences of a new concept has been one of the most fruitful 
sources of progress in the experimental sciences. For this reason, as a 



FIG. 5. Reproduction of a wood engraving of Boyle's first air pump, from his 
own book. 


case in point, the details of Boyle's reasoning merit careful consideration 
by anyone who attempts to understand the methods of modern science. 
Boyle's description of his seventeenth experiment now follows (the 
footnotes and the material enclosed in brackets have been added to 
assist the reader). 

Proceed we now to the mention of that experiment, whereof the 
satisfactory trial was the principal fruit I promised myself from our 
engine, it being then sufficiently known, that in the experiment de vacuo^ 
the quicksilver in the tube is wont to remain elevated, above the surface 
of that whereon it leans, about 27 digits [about 29.5 inches, as Boyle 
explains later]. I considered, that, if the true and only reason why the 
quicksilver falls no lower, be, that at that altitude the mercurial cylinder 
in the tube is in an equilibrium with the cylinder of air supposed to reach 
from the adjacent mercury to the top of the atmosphere [this is the con- 
ceptual scheme, suggested by Torricelli and elaborated by Pascal, that 
has been accepted ever since; note the use of the concept of equilibrium] ; 
then if this experiment could be tried out of the atmosphere, the quick- 
silver in the tube would fall down to a level with that in the vessel, since 
then there would be no pressure upon the subjacent, to resist the weight 
of the incumbent mercury. Whence I inferred (as easily I might) that 
if the experiment could be tried in our engine, the quicksilver would 
subside below 27 digits, in proportion to the exsuction of air, that should 
be made out of the receiver. For, as when the air is shut into the receiver, 
it doth (according to what hath above been taught) continue there as 
strongly compressed, as it did whilst all the incumbent cylinder of the 
atmosphere leaned immediately upon it; because the glass, wherein it Is 
penned up, hinders it to deliver itself, by an expansion of its parts, from 
the pressure wherewith it was shut up. So if we could perfectly draw 
the air out of the receiver, it would conduce as well to our purpose, as if 
we were allowed to try the experiment beyond the atmosphere. 

It should be noted that throughout the descriptions of his experi- 
ments Boyle spells everything out in great detail. That the pressure 
within the glass receiver is just as great after the receiver is closed off as 
it was before is obvious today, but it was far from clear at first. One of 
the first objections (see p. 7 and Fig. 3) to Torricdli's new ideas was 
that if the weight of the air on the outside mercury was responsible for 
the mercury's standing about 30 inches in the Torricellian tube, then 
sealing the whole apparatus inside a box should cause the mercury to 
fall, since the weight of the air would then only be that of the small 
amount in the surrounding box (Fig. 3). The error here, as Torricelli 
showed, is a confusion of weight and pressure. Boyle had probably 
heard of these arguments but had probably not read the account of 
them that is now available to us. 

20 CASE 1 

Wherefore (after having surmounted some little difficulties, which 
occurred at the beginning) the experiment was made after this manner: 
we took a slender and very curiously blown cylinder of glass, of near 
three foot in length, and whose bore had in diameter a quarter of an 
inch, wanting a hair's breadth: this pipe being hermetically sealed at 
one end [i.e., the glass being melted together so that no air could sub- 
sequently leak in], was, at the other, filled with quicksilver, care being 
taken in the filling, that as few bubbles as was possible should be left 
in the mercury. Then the tube being stopt with the finger and inverted, 
was opened, according to the manner of the experiment, into a some- 
what long and slender cylindrical box (instead of which we now are wont 
to use a glass of the same form) half filled with quicksilver: and so, the 
liquid metal being suffered to subside, and a piece of paper being pasted 
on level with its upper surface, the box and tube and all were by strings 
carefully let down into the receiver [through the opening at the top; 
see Fig. 6]: and then, by means of the hole formerly mentioned to be 
left in the cover, the said cover was slipt along as much of the tube as 
reached above the top of the receiver; and the interval, left betwixt the 
sides of the hole and those of the tube, was very exquisitely filled up with 
melted (but not over-hot) diachylon, and the round chink, betwixt the 
cover and the receiver, was likewise very carefully closed up: upon which 
closure there appeared not any change in the height of the mercurial 
cylinder, no more than if the interposed glass-receiver did not hinder the 
immediate pressure of the ambient atmosphere upon the inclosed air; 
which hereby appears to bear upon the mercury, rather by virtue of its 
spring than of its weight; since its weight cannot be supposed to amount 
to above two or three ounces, which is inconsiderable in comparison to 
such a cylinder of mercury as it would keep from subsiding. 

All things being thus in a readiness, the sucker [Fig. 4] was drawn 
down; and, immediately upon the egress of a cylinder of air out of the 
receiver, the quicksilver in the tube did, according to expectation, sub- 
side: and notice being carefully taken (by a mark fastened to the out- 
side) of the place where it stopt, we caused him that managed the pump 
to pump again, and marked how low the quicksilver fell at the second 
exsuction; but continuing this work, we were quickly hindered from 
accurately marking the stages made by the mercury, in its descent, be- 
cause it soon sunk below the top of the receiver, so that we could hence- 
forward mark it no other ways than by the eye. And thus, continuing 
the labour of pumping for about a quarter of an hour, we found ourselves 
unable to bring the quicksilver in the tube totally to subside; because, 
when the receiver was considerably emptied of its air, and consequently 
that little that remained grown unable to resist the irruption of the ex- 
ternal, that air would (in spight of whatever we could do) press in at 
some little avenue or other; and though much could not thereat get in, 
yet a little was sufficient to counterbalance the pressure of so small a 
cylinder of quicksilver, as then remained in the tube. 



Boyle subsequently used the length of such a column of mercury or its 
equivalent as a measure of the completeness of the vacuum he succeeded 
in producing in any experiment. We do the same today, but express 
our results in millimeters of mercury or in fractions of a millimeter of 
mercury. A well-constructed pump of Boyle's type today will hardly 
lower the pressure below a quarter of an inch of mercury. Pumps of a 

27 digits 

(29.5 inches) 

Paper scale 
on tube 

"Cylindrical box 
half filled with 
quicksilver' 1 

To pump 

FIG. 6. Diagram of Boyle's apparatus for the experiment of removing the air 
above the reservoir of a barometer ; W indicates "intervals*' filled with "diachylon." 
The pump was that shown in Fig. 4. 

different type are required to produce the high vacua used in the modern 
laboratory and in the manufacture of electric light bulbs and radio tubes. 

Now (to satisfy ourselves farther, that the falling of the quicksilver 
in the tube to a determinate height, proceedeth from the aequilibrium, 
wherein it is at that height with the external air, the one gravitating, 
the other pressing with equal force upon the subjacent mercury) we 
returned the key [Fig. 4] and let in some new air; upon which the 
mercury immediately began to ascend (or rather to be impelled upwards) 
in the tube, and continued ascending, till, having returned the key, it 
immediately rested at the height which it had then attained: and so, by 

22 CASE 1 

turning and returning the key, we did several times at pleasure impel it 
upwards, and check its ascent. And lastly, having given a free egress at 
the stop-cock to as much of the external air as would come in, the quick- 
silver was impelled up almost to its first height: I say almost, because it 
stopt near a quarter of an inch beneath the paper-mark formerly men- 
tioned; which we ascribed to this, that there was (as is usual in this ex- 
periment) some little particles of air engaged among those of the quick- 
silver; which particles, upon the descent of the quicksilver, did manifestly 
rise up in bubbles towards the top of the tube, and by their pressure, as 
well as by lessening the cylinder by as much room as they formerly took 
up in it, hindered the quicksilver from regaining its first height. 

This experiment was a few days after repeated, in the presence of those 
excellent and deservedly famous Mathematic Professors, Dr. Wallis, Dr. 
Ward, and Mr. Wren? who were pleased to honour it with their pres- 
ence; and whom I name, both as justly counting it an honour to be 
known to them, and as being glad of such judicious and illustrious wit- 
nesses of our experiment; and it was by their guess, that the top of the 
quicksilver in the tube was defined to be brought within an inch of the 
surface of that in the vessel. 

And here, for the illustration of the foregoing experiment, it will not 
be amiss to mention some other particulars relating to it. 

First then, when we endeavoured to make the experiment with the 
tube closed at one end with diachylon instead of an hermeticai seal, we 
perceived, that upon the drawing of some of the air out of the receiver, 
the mercury did indeed begin to fall, but continued afterwards to sub- 
side, though we did not continue pumping. When it appeared, that 
though the diachylon, that stopt the end of the tube, were so thick and 
strong, that the external air could not press it in, (as experience taught 
us that it would have done, if there had been but little of it;) yet the 
subtler parts of it were able (though slowly) to insinuate themselves 
through the very body of the plaister, which it seems was not of so close 
a texture, as that which we mentioned ourselves to have successfully 
made use of, in the experiment de vacuo some years ago. So that now 
we begin to suspect, that perhaps one reason, why we cannot perfectly 
pump out the air, may be, that when the vessel is almost empty, some 
of the subtler parts of the external air may, by the pressure of the atmos- 
phere, be strained through the very body of the diachylon into the re- 
ceiver. But this is only conjecture. 

8 These men were all at Oxford in the period 16551660 when the embryonic 
Royal Society was forming. Wren is the famous architect who rebuilt London 
after the great fire; Wallis and Ward were distinguished mathematicians. 
Wallis served the Parliamentary Armies in the Civil War by deciphering Royal- 
ist dispatches (a fact of which little was probably said after the Restoration in 
1660); Wren was "intruded" into All Souls College by a parliamentary com- 
mittee during the Cromwellian period. 


Here we see Boyle recording his experimental troubles. A tube sealed 
at the upper end with wax (diachylon) was often not leakproof. The 
conjecture that air might be a mixture of materials of differing degrees 
of "subtlety" is the basis of the experiments described in Sec. 4 of this 
Case History, and we see here how this thought could well have arisen 
from the experimental problem of obtaining airtight seals. 

Another circumstance of our experiment was this, that if (when the 
quicksilver in the tube was fallen low) too much ingress were, at the 
hole of the stop-cock, suddenly permitted to the external air; it would 
rush in with that violence, and bear so forcibly upon the surface of the 
subjacent quicksilver, that it would impel it up into the tube rudely 
enough to endanger the breaking of the glass. 

We formerly mentioned, that the quicksilver did not, in its descent, 
fall as much at a time, after the two or three first exsuctions of the air, 
as at the beginning. For, having marked its several stages upon the 
tube, we found, that at the first suck it descended an inch and %, and 
at the second an inch and %; and when the vessel was almost emptied, 
it could scarce at one exsuction be drawn down above the breadth of a 
barley-corn. And indeed we found it very difficult to measure, in what 
proportion these decrements of the mercurial cylinder did proceed; partly, 
because (as we have already intimated) the quicksilver was soon drawn 
below the top of the receiver; and partly because, upon its descent at each 
exsuction, it would immediately reascend a little upwards; either by 
reason of the leaking of the vessel at some imperceptible hole or other, 
or by reason of the motion of restitution in the air, which, being some- 
what compressed by the fall as well as weight of the quicksilver, would 
repel it a little upwards, and make it vibrate a little up and down, before 
they could reduce each other to such an aequilibrium as both might rest in. 

But though we could not hitherto make observations accurate enough, 
concerning the measures of the quicksilver's descent, to reduce them into 
any hypothesis, yet would we not discourage any from attempting it; 
since, if it could be reduced to a certainty, it is probable, that the discovery 
would not be unuseful. 

And, to illustrate this matter a little more, we will add, that we made 
a shift to try the experiment in one of our above mentioned [in a section 
of Boyle's book not reproduced herein] small receivers, not containing a 
quart; but (agreeably to what we formerly observed) we found it as diffi- 
cult to bring this to be quite empty as to evacuate the greater; the least 
external air that could get in (and we could not possibly keep it all per- 
fectly out) sufficing, in so small a vessel, to display a considerable pressure 
upon the surface of the mercury, and thereby hinder that in the tube 
from falling to a level with it* But this is remarkable, that having two or 
three times tried the experiment in a small vessel upon the very first cylin- 
der of air that was drawn out of the receiver, the mercury fell in the tube 
1 8 inches and a half, and another trial 19 inches and a half. . . . 

24 CASE 1 

The ratio of the volume of the receiver i.e., the vessel being 
evacuated to the volume of the cylinder of the pump determines the 
effects of each stroke of the piston. With Boyle's large receiver, probably 
this ratio was something like 20 to i. Each stroke of the piston would 
thus reduce the pressure by about 1/21 which for the first stroke would 
mean a fall in mercury level of about i l / 2 inch; with a small receiver 
whose volume was less than that of the pump cylinder the pressure 
would be reduced by more than one half (by 1 8 or 19 inches, Boyle 
records) . 

The next few paragraphs of the book, which are omitted here, discuss 
Boyle's futile attempts to reason in numerical terms about the phe- 
nomena he had observed. He was unable to reduce his qualitative 
observations to a quantitative basis; he was unable to use the new 
conceptual scheme for he did not see at that time that if two vessels of 
equal volume, one full of air at atmospheric pressure, the other essen- 
tially empty, are connected, the pressure becomes the same in both 
vessels, namely, half of what it originally was in the first vessel. 

For farther confirmation of what hath been delivered, we likewise tried 
the experiment in a tube of less than two foot long: and, when there was 
so much air drawn out of the vessel, that the remaining air was not able 
to counterbalance the mercurial cylinder, the quicksilver in the tube sub- 
sided so visibly, that (the experiment being tried in the little vessel lately 
mentioned) at the first suck it fell above a span, and was afterwards 
drawn lower and lower for a little while; and the external air being let 
in upon it, impelled it up again almost to the top of the tube: so little 
matters it, how heavy or light the cylinder of quicksilver to subside is, 
provided its gravity overpower the pressure of as much external air as 
bears upon the surface of that mercury into which it is to fall. 

In other words, it is unnecessary to start with a barometer in this 
experiment, for a short inverted tube filled with mercury will suffice. 
This is the equivalent of the lower portion of the Torricellian tube; it 
is far more convenient than the long tube, and the simplest vacuum 
gauges used today in chemical and physical laboratories are constructed 
in this way. 

Lastly, we also observed, that if (when the mercury in the tube had 
been drawn down, and by an ingress permitted to the external air, im- 
pelled up again to its former height) there were some more air thrust 
up by the help of the pump into the receiver, the quicksilver in the tube 
would ascend much above the wonted height of 27 digits, and immedi- 
ately upon the letting out of that air would fall again to the height it 
rested at before. [Here Boyle pumps air into the receiver and shows that 
the increased pressure causes the height of the mercury to increase be- 
yond the barometric height,] 


Your Lordship will here perhaps expect, that as those, who have 
treated of the Torricellian experiment, have for the most part maintained 
the affirmative, or the negative of that famous question, whether or no 
that noble experiment infer a vacuum? so I should on this occasion in- 
terpose my opinion touching that controversy; or at least declare, whether 
or no, in our engine, the exsuction of the air do prove the place deserted 
by the air sucked out to be truly empty, that Is, devoid of all corporeal 
substance. But besides that I have neither the leisure, nor the ability, to 
enter into a solemn debate of so nice a question; your Lordship may, if 
you think it worth the trouble, in the Dialogues not long since referred 
to, find the difficulties on both sides represented, which then made me 
yield but a very wavering assent to either of the parties contending about 
the question: nor dare I yet take upon me to determine so difficult a 

For on the one side it appears, that notwithstanding the exsuction of 
the air, our receiver may not be destitute of all bodies, since any thing 
placed in it, may be seen there; which would not be, if it were not per- 
vious to those beams of light, which rebounding from the seen object 
to our eyes, affect us with the sense of it: and that either these beams are 
corporeal emanations from some lucid body, or else at least the light 
they convey doth result from the brisk motion of some subtle matter, I 
could, if I mistake not, sufficiently manifest out of the Dialogues above- 
mentioned, if I thought your Lordship could seriously imagine that light 
could be conveyed without, at least, having (if I may so speak) a body 
for its vehicle. 

In the eighteenth and nineteenth centuries, as in the seventeenth, it 
would have been taken for granted that light was either a beam of 
particles that would pass through glass or else a motion in a medium 
that pervaded glass. The latter view seemed to be established by experi- 
ment early in the nineteenth century and the medium was given the 
name "luminiferous ether" or "ether" (not to be confused with the 
anaesthetic with the same name). The same medium could be invoked 
to explain the action of magnetism (see Boyle's next two paragraphs). 
This medium was imagined to be far too subtle, to use Boyle's phrase, to 
be subject to mechanical rarefaction or compression as is air. As the 
study of radiant energy proceeded, the conceptual scheme that postu- 
lated ether as a medium became inadequate because it failed to account 
for certain phenomena. The answer to the question raised by Boyle's 
contemporaries, if a vacuum is really empty how can you see through 
it, cannot be given today in terms of any one simple conceptual scheme. 
Modern views simply challenge the assumption that seemed so obvious 
to Boyle and many later scientists, namely, that light must for its con- 
veyance require "a body for its vehicle." 

26 CASE 1 

By the sixteenth experiment, it also appears that the closeness of our 
receiver hinders it not from admitting the effluvia of the load-stone; 6 
which makes it very probable that it also freely admits the magnetical 
steams of the earth; concerning which, we have in another treatise en- 
deavoured to manifest that numbers of them do always permeate our air. 

But on the other side it may be said, that as for the subtle matter which 
makes the objects enclosed in our evacuated receiver, visible, and the 
magnetical effluvia of the earth that may be presumed to pass through 
it, though we should grant our vessel not to be quite devoid of them, yet 
we cannot so reasonably affirm it to be replenished with them, as we 
may suppose, that if they were gathered together into one place without 
intervals between them, they would fill but a small part of the whole 
receiver. As in the thirteenth experiment, a piece of match was incon- 
siderable for its bulk, whilst its parts lay close together, that afterwards 
(when the fire had scattered them into smoke) seemed to replenish all 
the vessel. For (as elsewhere our experiments have demonstrated) both 
light and the effluvia of the load-stone may be readily admitted into a 
glass, hermetically sealed, though before their admission, as full of air 
as hollow bodies here below are wont to be; so that upon the exsuction 
of the air, the large space deserted by it, may remain empty, notwith- 
standing the pretence of those subtle corpuscles, by which lucid and 
magnetical bodies produce their effects]. 

In short, "those subtle corpuscles, by which lucid and magnetical 
bodies produce their effects" are quite independent o the particles that 
compose the air. This may be considered a preview of the doctrine of 
the ether as it was expounded by all scientists 75 years ago. The relevance 
of the experiment with the match is not obvious. The thirteenth experi- 
ment consisted in allowing the smoke from a "slow match" a slow- 
burning material used for ignition of cannon to fill an evacuated 
receiver, which it did, of course, rapidly. This phenomenon inspired 
Boyle perhaps unduly; he saw in it a visualization of the way "subtle 
material" such as air will expand at once and fill a space; he likewise 
recognized that a very minute amount of match was consumed in 
producing enough smoke to fill a large receiver. Therefore, he argues 
that the still more subtle corpuscles that convey light need be of but 
little bulk if solidified all together. 

The controversy between the Vacuists and the Plenists, referred to in 
the next paragraph, goes back at least to Aristotle. In the form referred 

6 What we would now call the field of a magnet. In short, a magnet a piece 
of the naturally occurring magnetized iron ore is called a loadstone will 
exert a force on iron placed in a vacuum. This had been demonstrated by the 
Florentine experiments and also by von Guericke before Boyle's experiments. 
The phrase "magnetical steams of the earth" in the same sentence refers to the 
earth's magnetic field, about which Boyle speculated in another book. 


to by Boyle, it continued until the close of the century. The plenists con- 
fused the "subtle material the vehicle of light" with air. To them the 
explanation of why water will not run out of an inverted bottle with 
a narrow neck (unless air is shaken in or another opening made) was 
as follows : if the water comes out, the surrounding medium must be 
displaced, and it can be displaced only if there is somewhere for it to 
go. If a second opening is provided in the bottle, the displaced medium 
can enter; therefore, the water runs out. 

According to the Plenists the world was full, by definition; a 
vacuum was unthinkable; these were the postulates of their position. 
A further premise of their position, but one not recognized, was that the 
medium was essentially incompressible; otherwise the water might run 
out of an inverted bottle by compressing rather than displacing the 
surrounding medium. It may be left to the reader to see how the posi- 
tion of the Plenists became untenable in the light of the Torricellian 
experiment unless some additional and arbitrary assumptions were 

And as for the allegations above-mentioned, they seemed to prove but 
that the receiver devoid of air, may be replenished with some etherial 
matter, as some modern Naturalists write of, but not that it really is so. 
And indeed to me it yet seems, that as to those spaces which the Vacuists 
would have to be empty, because they are manifestly devoid of air and 
all grosser bodies; the Plenists (if I may so call them) do not prove that 
such spaces are replenished with such a subtle matter as they speak of, 
by any sensible effects, or operations of it (of which divers new trials 
purposely made, have not yet shewn me any) but only conclude that 
there must be such a body, because there cannot be a void. And the 
reason why there cannot be a void, being by them taken, not from any 
experiments, or phenomena of nature, that clearly and particularly prove 
their hypothesis, but from their notion of a body, whose nature, accord- 
ing to them, consisting only in extension (which indeed seems the prop- 
erty most essential to, because inseparable from a body) to say a space 
devoid of body, is, to speak in the schoolmen's phrase, a contradiction in 
adjecto. This reason, I say, being thus desumed, seems to make the con- 
troversy about a vacuum rather a metaphysical, than a physiological ques- 
tion; 7 which therefore we shall here no longer debate, finding it very 
difficult either to satisfy Naturalists with this Cartesian notion of a body, 
or to manifest wherein it is erroneous, and substitute a better in its stead. 

But though we are unwilling to examine any farther the inferences 
wont to be made from the Torricellian experiment, yet we think it not 

7 This curious use of the word "physiological" is now obsolete; in the seven- 
teenth century the word "physiology" was sometimes used as equivalent to 
natural science. 

28 CASE 1 

impertinent to present your Lordship with a couple of advertisements 
concerning it. 

First then, if in trying the experiment here or elsewhere, you make use 
of the English measures that mathematicians and tradesmen are here 
wont to employ, you will, unless you be forewarned of it, be apt to 
suspect that those that have written of the experiment have been mis- 
taken. For whereas men are wont generally to talk of the quicksilver's 
remaining suspended at the height of between six or seven and twenty 
inches; we commonly observed, when divers years since we first were 
solicitous about this experiment, that the quicksilver in the tube rested 
at about 29 inches and a half above the surface of the restagnant quick- 
silver in the vessel, which did at first both amaze and perplex us, because 
though we held it not improbable that the difference of the grosser 
English air, and that of Italy and France, might keep the quicksilver 
from falling quite as low in this colder, as in those warmer climates; 
yet we could not believe that that difference in the air should alone be 
able to make so great an one in the heights of the mercurial cylinders; 
and accordingly upon enquiry we found, that though the various density 
of the air be not to be overlooked in this experiment, yet the main reason 
why we found the cylinder of mercury to consist of so many inches, was 
this, that our English inches are somewhat inferior in length to the digits 
made use of in foreign parts, by the writers of the experiment. 8 

The next thing I desire your Lordship to take notice of, is, that the 
height of the mercurial cylinder is not wont to be found altogether so 
great as really it might prove, by reason of the negligence or incogitancy 
of most that make the experiment. For oftentimes upon the opening 
of the inverted tube into the vesselled mercury, you may observe a 
bubble of air to ascend from the bottom of the tube through the sub- 
siding quicksilver to the top; and almost always you may, if you look 
narrowly, take notice of a multitude of small bubbles all along the in- 
side of the tube betwixt the quicksilver and the glass; (not now to men- 
tion the particles of air that lie concealed in the very body of the mer- 
cury:) many of which, upon the quicksilver's forsaking the upper part 
of the tube, do break into that deserted space where they find little or no 
resistance to their expanding of themselves. [It is difficulties such as this 
that are the basis of one's skepticism about the accuracy of Perier's re- 
ports (see p. 8).] Whether this be the reason, that upon the application 
of warm bodies to the emptied part of the tube, 9 the subjacent mercury 
would be depressed somewhat lower, we shall not determine; though it 

8 Difficulties of this sort have led to an international agreement on standards 
of measurement. The accuracy required in modern experiments has meant 
that providing standards has become a rather elaborate matter. 

9 We are now quite certain that this is the reason. To the extent that there is air 
in the space above the mercury in the Torricellian tube, warming and cooling 
this space will affect the height of the column since air expands and contracts 
with changes in temperature, a fact well known by 1660. 


seem very probable, especially since we found, that, upon the application 
of linen cloths dipped in water, to the same part of the tube, the quick- 
silver would somewhat ascend; as if the cold had condensed the im- 
prisoned air (that pressed upon it) into a lesser room. But that the de- 
serted space is not wont to be totally devoid of air, we were induced to 
think by several circumstances: for when an eminent mathematician, and 
excellent experimenter, had taken great pains and spent much time in 
accurately filling up a tube of mercury, we found that yet there remained 
store of inconspicuous bubbles, by inverting the tube, letting the quick- 
silver fall to its wonted height; and by applying (by degrees) a red-hot 
iron to the outside of the tube, over against the upper part of the mer- 
curial cylinder, (for hereby the little unheeded bubbles, being mightily 
expanded, ascended in such numbers, and so fast to the deserted space, 
that the upper part of the quicksilver seemed, to our wonder, to boil.) 
We farther observed, that in the trials of the Torricellian experiment, we 
have seen made by others, and (one excepted) all our own, we never 
found that, upon the inclining of the tube, the quicksilver would fully 
reach to the very top of the sealed end: which argued, that there was 
some air retreated thither that kept the mercury out of the unreplenished 
space. [This is the forerunner of many such methods of checking on the 
performance of an apparatus. If Perier had reported that he had made 
this test in each instance, one would be more inclined to take seriously 
the reported accuracy of his results. But despite Perier's statement that he 
"carefully rid the tube of air," one remains skeptical of his ability to 
repeat the Torricellian experiment with an accuracy of a twelfth of an 

If your Lordship should now demand what are the best expedients to 
hinder the intrusion of the air in this experiment; we must answer, that 
of those which are easily intelligible without ocular demonstration; we 
can at present suggest, upon our own trials, no better than these. First, 
at the open end of the tube the glass must not only be made as even at 
the edges as you can, but it is very convenient (especially if the tube be 
large) that the bottom be every way bent inwards, that so the orifice 
not much exceeding a quarter of an inch in diameter, may be the more 
easily and exactly stopped by the experimenter's finger; between which 
and the quicksilver, that there may be no air intercepted (as very often 
it happens that there is) it is requisite that the tube be filled as full as 
possibly it can be, that the finger which is to stop it, pressing upon the 
accumulated and protuberant mercury, may rather throw down some, 
than not find enough exactly to keep out the air. It is also an useful 
and compendious way not to fill the tube at first quite of mercury, but 
to leave near the top about a quarter of an inch empty; for if you then 
stop the open end with your finger, and invert the tube, that quarter of 
an inch of air will ascend in a great bubble to the top, and in its passage 
thither, will gather up all the little bubbles, and unite them with itself 
into one great one; so that if by rein verting the tube, you let that bubble 
return to the open end of it, you will have a much closer mercurial cylin- 

30 CASE 1 

der than before, and need but to add a very little quicksilver more to fill 
up the tube exactly. And lastly, as for those lesser and inconspicuous 
parcels of air which cannot this way be gleaned up, you may endeavour, 
before you invert the tube, to free the quicksilver from them by shaking 
the tube, and gently knocking on the outside of it, after every little parcel 
of quicksilver which you pour in; and afterwards, by forcing the small 
latitant bubbles of air to disclose themselves and break, by imploying a 
hot iron in such manner as we lately mentioned. I remember that by 
carefully filling the tube, though yet it were not quite free from air, we 
have made the mercurial cylinder reach to 30 inches and above an eighth, 
and this in a very short tube: which we therefore mention, because we 
have found, by experience, that in short tubes a little air is more prejudi- 
cial to the experiment than in long ones, where the air having more 
room to expand itself, doth less potently press upon the subjacent mercury. 

Note the type of extremely helpful suggestions given by Boyle for 
the benefit of others who wished likewise to experiment; before the 
publication of this book in 1660 few if any instances are on record of a 
similar concern with the difficulties of other experimenters except in 
so far as the recipes of the alchemists can be considered in this category. 


Boyle's published record of two experiments on air as a medium 
for transmitting sound is given in this section. The first is Experiment 
27 in his book of 1660; the second is Experiment 41 of his second book 
on pneumatics, published in 1669. 

Boyle's description o his twenty-seventh experiment in his account 
of 1660 follows. 

That the air is the medium, whereby sounds are conveyed to the ear, 
hath been for many ages, and is yet the common doctrine of the schools. 
But this received opinion hath been of late opposed by some philosophers 
upon the account of an experiment made by the industrious Kircher, 
and other learned men; who have (as they assure us) observed, that if 
a bell, with a steel clapper, be so fastened to the inside of a tube, that 
upon the making the experiment de vacuo [see footnote i] with that tube, 
the bell remained suspended in the deserted space at the upper end of 
the tube: and if also a vigorous load-stone be applied on the outside of 
the tube to the bell, it will attract the clapper, which, upon the removal 
of the load-stone falling back, will strike against the opposite side of the 
bell, and thereby produce a very audible sound; whence divers have con- 
cluded, that it is not the air, but some more subtle body, that is the 
medium of sounds. But because we conceived, that, to invalidate such a 
consequence from this ingenious experiment, (though the most luciferous 
that could well be made without some such engine as ours) some things 


might be speciously enough alledged; we thought fit to make a trial or 
two, in order to the discovery of what the air doth in conveying of sounds, 
reserving divers other experiments triable in our engine concerning 
sounds, till we can obtain more leisure to prosecute them. Conceiving it 
then the best way to make our trial with such a noise, as might not be 
loud enough to make it difficult to discern slighter variations in it, but 
rather might be, both lasting (that we might take notice by what degrees 
it decreased) and so small, that it could not grow much weaker without 
becoming imperceptible; we took a watch, whose case we opened, that 
the contained air might have free egress into that of the receiver. And 
this watch was suspended in the cavity of the vessel only by a pack-thread, 
as the unlikeliest thing to convey a sound to the top of the receiver; and 
then closing up the vessel with melted plaister, we listened near the sides 
of it, and plainly enough heard the noise made by the balance. [Boyle 
clearly recognized the importance of controlling the conditions in an 
experiment. The method of supporting the source of the noise at first 
sight appears irrelevant. On further reflection, however, it is clear that 
the sound might be transmitted through this support. If so, a thread 
seemed less likely to convey sound than a metal or wooden support. To 
make sure that a watch so suspended by a thread in air could still be 
heard, Boyle proceeded to determine whether he could hear the watch 
before he pumped out the air.] Those also of us, that watched for that 
circumstance, observed, that the noise seemed to come directly in a streight 
line from the watch unto the ear. And it was observable to this purpose, 
that we found a manifest disparity of noise, by holding our ears near 
the sides of the receiver, and near the cover of it: which difference seemed 
to proceed from that of the texture of the glass, from the structure of the 
cover (and the cement) through which the sound was propagated from 
the watch to the ear. But let us prosecute our experiment [that is, let us 
start pumping the air out of the receiver in which the watch is suspended 
by a thread]. The pump after this being employed, it seemed, that from 
time to time the sound grew fainter and fainter; so that when the re- 
ceiver was emptied as much as it used to be for the foregoing experi- 
ments, neither we, nor some strangers, that chanced to be then in the 
room, could, by applying our ears to the very sides, hear any noise from 
within; though we could easily perceive, that by the moving of the hand, 
which marked the second minutes, and by that of the balance, that the 
watch neither stood still, nor remarkably varied from its wonted motion. 
And to satisfy ourselves farther, that it was indeed the absence of the 
air about the watch, that hindered us from hearing it, we let in the ex- 
ternal air at the stop-cock; and then though we turned the key and stopt 
the valve, yet we could plainly hear the noise made by the balance, though 
we held our ears sometimes at two foot distance from the outside of the 
receiver; and this experiment being reiterated into another place, suc- 
ceeded after the like manner. Which seems to prove, that whether or no 
the air be the only, it is at least the principal medium of sounds. [A very 
cautious interpretation of the experimental findings. Boyle recognizes 

32 CASE 1 

that there might be two or more media by which sound was transmitted, 
but if so the second medium did not play the principal part in the usual 
case. His search for a second more "subtle medium" is recorded in Sec. 4.] 
And by the way it Is very well worth noting, that in a vessel so well 
closed as our receiver, so weak a pulse as that the balance of a watch, 
should propagate a motion to the air in a physically streight line, not- 
withstanding the interposition of so close a body as glass, especially glass 
of such thickness as that of our receiver; since by this it seems the air 
imprisoned in the glass must, by the motion of the balance, be made to 
beat against the concave part of the receiver, strongly enough to make its 
convex part beat upon the contiguous air, and so propagate the motion to 
the listner's ears. [Boyle here reverts to a discussion of the fact that before 
the air was pumped out, one could hear the watch imprisoned in the 
receiver.] I know this cannot but seem strange to those, who, with an 
eminent modern philosopher, will not allow, that a sound, made in the 
cavity of a room, or other place so closed, that there is no intercourse 
betwixt the external and internal air, can be heard by those without, un- 
less the sounding body do immediately strike against some part of the 
inclosing body. But not having now time to handle controversies, we shall 
only annex, that after the foregoing experiment, we took a bell of about 
two inches in diameter at the bottom, which was supported in the midst 
of the cavity of the receiver by a bent stick, which by reason of its spring 
pressed with its two ends against the opposite parts of the inside of the 
vessel: in which, when it was closed up, we observed, that the bell seemed 
to sound more dead than it did when just before it sounded in the open 
air. And yet, when afterwards we had (as formerly) emptied the re- 
ceiver, we could not discern any considerable change (for some said they 
observed a small one) in the loudness of the sound. Whereby it seemed, 
that though the air be the principal medium of sound, yet either a more 
subtle matter may be also a medium of it, or else an ambient body, that 
contains but very few particles of air, in comparison of those it is easily 
capable of, is sufficient for that purpose. And this, among other things, 
invited us to consider, whether in the above-mentioned experiment made 
with the bell and the load-stone, there might not in the deserted part of 
the tube remain air enough to produce a sound; since the tubes for the 
experiment de vacuo (not to mention the usual thinness of the glass) 
being seldom made greater than is requisite, a little air might bear a not 
inconsiderable proportion to the deserted space: and that also, in the 
experiment de vacuo^ as it is wont to be made, there is generally some 
little air, that gets in from without, or at least store of bubbles, that arise 
from the body of the quicksilver, or other liquor itself, observations 
heedfully made have frequently informed us; and it may also appear, 
by what hath been formerly delivered concerning the Torricellian experi- 

Experimentation with a Torricellian vacuum was certainly difficult. 
We now know that the two major sources of error in the study of the 



propagation of sound in a vacuum are (i) the presence of air in the 
evacuated space, (ii) the transmission of sound by the solid support of 
the source of the sound. 

We now turn to the record of some experiments performed some six 
or seven years later with the aid of the second and improved model of 
Boyle's pneumatic engine. Boyle's original drawing of this arrangement 
is reproduced in Fig. 7. Here he shows a still more convenient method 

FIG. 7. Boyle's second air pump. This illustration is partly diagrammatic: the 
iron plate CDEF onto which the glass receiver is sealed is imagined to be cut 
away so as to show the tube AB connecting the receiver with the pump through 
the valve HG; the structure of the pump is not indicated, but was essentially the 
same as in the first model. 

of performing experiments in vacuo. For in this case the apparatus to 
be studied rests on an iron plate under a bell jar, which is then sealed by 
wax to the plate and the air evacuated through a hole in the bottom of 
the plate connected by a tube to the pump. This is still the usual arrange- 
ment in lecture-table demonstrations of experiments in a vacuum. 

34 CASE I 

EXPERIMENT 41 [of the book entitled A Continuation of New Experi- 
ments Physico-Mechanical Touching the Spring and Weight of the Air, 
and their Effects, published in 1669]. 

About the propagation of sounds in the exhausted receiver. 

To make some further observation than is mentioned in the published 
experiments, about the production and conveying of sounds in a glass 
whence the air is drawn out, we employed a contrivance, of which, be- 
cause we make use of it in divers other experiments, it will be requisite 
to give your lordship here some short description. 

We caused to be made at the turner's a cylinder of box, or the like close 
and firm wood, and of a length suitable to that of the receiver it was to 
be employed in. Out of the lower basis of this cylinder (which might be 
about an inch and a half in diameter) there came a smaller cylinder or 
axle-tree, not a quarter so thick as the other, and less than an inch long; 
this was turned very true, that it might move to and fro; or, as the trades- 
men call it, ride very smoothly in a little ferrule or ring of brass, that was 
by the same turner made for it in the midst of the fixed trencher (as 
we call a piece of solid wood, shaped like a mill-stone) being four or 
five inches, more or less (according to the wideness of the receiver) in 
breadth, and between one and two in thickness; and in a large and round 
groove or gutter, purposely made in the lower part of this trencher, I 
caused as much lead as would fill it up to be placed and fastened, that it 
might keep the trencher from being easily moved out of its place or 
posture, and in the upper part of this trencher it was intended that holes 
should be made at such places as should be thought fit, to place bodies 
at several distances as occasion should require. The upper basis of the 
cylinder had also coming out of the midst of it another axle-tree, but 
wider than the former, that, into a cavity made in it, it might receive 
the lower end of the turning-key divers times already mentioned, to 
which it was to be fastened by a slender peg of brass thrust through two 
correspondent holes, the one made in the key, and the other in the 
newly-mentioned socket (if I may so call it) of the axle-tree. Besides all 
which, there were divers horizontal perforations bored here and there in 
the pillar itself, to which this axis belonged, which pillar we shall, to 
avoid ambiguity, call the vertical cylinder. The general use of this con- 
trivance (whose other parts need not to be mentioned before the experi- 
ments where they are employed) is, that the end of the turning-key being 
put into the socket, and the lower axis of the vertical cylinder into the 
trencher, by the motion of the key a body fastened at one of the holes to 
the cylinder may be approached to, or removed from, or made to rub or 
strike against another body fastened in a convenient posture to the upper 
part of the trencher. [The apparatus here described was depicted by Boyle 
as shown in Fig. 8.] 

To come now to our trial about sounds, we caused a hand-bell (whose 
handle and clapper were taken away) to be fastened to a strong wire, 
that, one end of the wire being made fast in the trencher, the other end, 



which was purposely bent downwards, took hold of the bell. In another 
hole made in the circumference of the same trencher was wedged in 
(with a wooden peg) a steel-spring, to whose upper part was tied a gad 
of iron or steel, less than an inch long, but of a pretty thickness. The 
length of this spring was such, as to make the upper part of the hammer 
(if I may so call the piece of iron) of the same height with the bell, 

FIG. 8. Wood engraving from Boyle's book, showing the "cylinder or axle 
tree" connected to a "turning key'* which enabled Boyle to strike a bell in a 

and the distance of the spring from the bell was such, that when it was 
forced back the other way, it might at its return make the hammer strike 
briskly upon the outside of the bell. 

Boyle used a brass cover on some of his bell jars, thus enabling him 
to have a "key," fitted through a carefully constructed opening, which 
could be turned without admitting air. The difficulties of having this 
key turn in an airtight bearing are very great. There must have been a 
considerable amount of leakage in the apparatus. In the third paragraph 
below, Boyle describes an experimental precaution against leakage of 
air around the key. If he had at this time developed instruments for 
measuring the air pressure inside an evacuated vessel (as he later did), 
he could have carried out all these experiments with more assurance. 
He would then have made his observations at the same low pressure, 
say that corresponding to i inch-of-mercury. 

36 CASE 1 

The trencher being thus furnished and placed in a capped receiver 
(as you know, for brevity sake, we use to call one that is fitted with 
one or other of the brass covers, often mentioned already) the air was 
diligently pumped out; and then, by the help of the turning-key, the 
vertical cylinder was made to go round, by which means as often as 
either of a couple of stiff wires or small pegs that were fastened at right 
angles into holes, made not far from the bottom of the cylinder, passed 
(under the bell, and) by the lately mentioned spring, they forcibly did 
in their passage bend it from the bell, by which means, as soon as the 
wire was gone by, and the spring ceased to be pressed, it would fly back 
with violence enough to make the hammer give a smart stroke upon 
the bell: and by this means we could both continue the experiment at 
discretion, and make the percussions more equally strong, than it would 
otherwise have been easy to do. 

The event of our trial was, that, when the receiver was well emptied, 
it sometimes seemed doubtful, especially to some of the by-standers, 
whether any sound were produced or no; but to me, for the most part, 
it seemed, that after much attention I heard a sound, that I could but just 
hear; and yet, which is odd, methought it had somewhat of the nature of 
shrilness in it, but seemed (which is not strange) to come from a good 
way off. Whether the often turning of the cylindrical key kept the re- 
ceiver from being so stanch as else it would have been, upon which score 
some little air might insinuate itself, I shall not positively determine; 
but to discover what Interest the presence or the absence of the air might 
have in the loudness or lowness of the sound, I caused the air to be let 
into the receiver, not all at once, but at several times, with competent 
intervals between them; by which expedient it was easy to observe, that 
the vertical cylinder being still made to go round, when a little air was 
let in, the stroke of the hammer upon the bell (that before could now 
and then not be heard, and for the most part be but very scarcely heard) 
began to be easily heard; and when a little more air was let in, the 
sound grew more and more audible, and so increased, until the receiver 
was again replenished with air; though even then (that we omit not that 
phenomenon) the sound was observed to be much less loud than when 
the receiver was not interposed between the bell and the ear. 

And whereas in the already published physico-mechanical experiments 
[Experiment 27, p. 30], I acquainted your lordship with what I observed 
about the sound of an ordinary watch in the exhausted receiver, I shall 
now add, that that experiment was repeated not long since, with the 
addition of suspending in the receiver a watch with a good alarum, which 
was purposely so set, that it might, before it should begin to ring, give 
us time to cement on the receiver very carefully, exhaust it very dili- 
gently, and settle ourselves in a silent and attentive posture. And to make 
this experiment in some respect more accurate than the others we made 
of sounds, we secured ourselves against any leaking at the top, by imploy- 
ing a receiver that was made all of one piece of glass (and consequently 


had no cover cemented on to it) being furnished only within (when it 
was first blown) with a glass-knob or button, to which a string might 
be tied. And because it might be suspected, that if the watch were sus- 
pended by its own silver chain, the tremulous motion of its sounding 
bell might be propagated by that metalline chain [the same question 
that arose in Experiment 27] to the upper part of the glass, to obviate 
this as well as we could, we hung the watch, not by its chain, but a very 
slender thread, whose upper end was fastened to the newly mentioned 

These things being done, and the air being carefully pumped out, we 
silently expected the time, when the alarum should begin to ring, which 
it was easy to know by the help of our other watches; but not hearing 
any noise so soon as we expected, it would perhaps have been doubted 
whether the watch continued going, if for prevention we had not ordered 
the matter so, that we could discern it did not stand still: wherefore I 
desired an ingenious gentleman to hold his ear just over the button at 
which the watch was suspended, and to hold it also very near to the 
receiver; upon which he told us, that he could perceive, and but just 
perceive something of sound that seemed to come from far; though neither 
we that listened very attentively near other parts of the receiver, nor he, 
if his ears were no more advantaged in point of position than ours, were 
satisfied that we heard the watch at all Wherefore ordering some air to 
be let in, we did, by the help of attention, begin to hear the alarum, whose 
sound was odd enough, and, by returning the stop-cock to keep any more 
air from getting in, we kept the sound thus low for a pretty while, after 
which a little more air, that was permitted to enter, made it become more 
audible; and when the air was yet more freely admitted, the by-standers 
could plainly hear the noise of .the yet continuing alarum at a considerable 
distance from the receiver. [By using a thread for a support, and eliminat- 
ing the turning key (and thus the leakage), Boyle has finally succeeded in 
reducing the sound to a point where it cannot be heard. When air is 
allowed to enter the receiver, the sound is readily audible. The evidence 
that air is the medium for transmitting sound is now quite convincing.! 

From what has hitherto been related, we may learn what is to be 
thought of what is delivered by the learned Mersennus in that book 
of his Harmonicks, where he makes this to be the first proposition. 
Sonus a campanis, vel ahis corporibus non solum producitur in illo vacuo 
(quicquid tandem illud sit) quod sit in tubis hydrargyro plenis, posteaque 
depletis, sed etiam idem acumen, quod in acre libero vd clause penitus 
observatur & auditur^ For the proof of which assertion, not long after, 

10 Father Mersenne, the indefatigable reporter of experimental philosophy 
through whom Pascal first learned of Torricelli's experiment Boyle seems lo 
be referring to his report of the Florentine work on the propagation of sound 
in a vacuum carried out with a Torricellian vacuum. 

11 A free translation of the Latin passage is as follows: Not only is the sound of 
even the shrillest bells produced in the vacuum (whatever that may finally turn 

38 CASE 1 

he speaks thus: porro variis tubis, quorum extremis lagence vitrece ad- 
glutinantur, observari campanas in illo vacua appensas propriisque malleis 
percussas idem penitus acumen retmere, quod in acre libero habent: 
atque soni magnitudinem ei sono, qui sit in acre quern tubus clausus in- 
cludit) nihil cedere. 12 But though our experiments sufficiently manifest, 
that the presence or absence of the common air is of no small importance 
as to the conveying of sounds, and that the interposition of glass may 
sensibly weaken them; yet so diligent and faithful a writer as Mersennus 
deserves to be favourably treated; and therefore I shall represent on his 
behalf, that what he says may well enough have been true, as far as could 
be gathered from the trials he made. For, first, it is no easy matter, espe- 
cially for those that have not peculiar and very close cements, to keep the 
air quite out for any considerable time in vessels consisting of divers pieces, 
such as he appears to have made use of; and next, the bigness of the bell 
in reference to the capacity of the exhausted glass, and the thickness of 
the glass, and the manner whereby the bell was fastened to the inside of 
the glass, and the hammer or clapper was made to strike, may much vary 
the effect of the trial, for reasons easy to be gathered out of the past dis- 
course, and therefore not needful to be here insisted on. And upon this 
account we chose to make our experiment with sounds that should not 
be strong or loud, and to produce them after such a manner, as that as 
little shaking as could be might be given by the sounding body to the 
glass it was included in. 


We have already noted Boyle's concern with the possibility 
that in addition to the air which he could pump out of his receivers, 
there might be present in the atmosphere more subtle material that 
would pass through holes too small to allow the passage of air. Such 
a medium, which had been postulated by Descartes and to some degree 
confused with air by subsequent proponents of the Plenist doctrine, 
might conceivably be still present in an evacuated receiver and still sub- 
ject to movement by mechanical means. To test this possibility, Boyle 
contrived a series of ingenious experiments some of which are described 
in the following account of Experiments 38, 39, and 40 of his book of 
1669. All these experiments yielded negative results. 

out to be) which he makes by filling tubes with mercury and then pouring 
them off [i.e., by performing the Torricellian experiment], but also the 
pitch is observed to be the same as that heard in free but entirely enclosed air. 
12 "Further, bells hung in the vacuum, produced in inverted glass flagons to 
whose mouths tubes have been glued, are observed when struck with their 
own hammers to maintain the same pitch that they would have in the open 
air. Also it is noted that the loudness of the tone is no less than that produced 
by the bells when the tubes contain air." 


EXPERIMENT 38 [from Boyle's Continuation of 1669] 

About an attempt to examine the motions and sensi- 
bility of the Cartesian Materia subtilis, or the jEther, 
with a pair of bellows made of a bladder, in the ex- 
hausted receiver. 

I will not now discuss the controversy betwixt some of the modern 
atomists and the Cartesians; the former of whom think, that betwixt 
the earth and the stars, and betwixt these themselves, there are vast 
tracts of space that are empty, save where the beams of light do pass 
through them; and the latter of whom tell us, that the intervals betwixt 
the stars and planets, among which the earth may perhaps be reckoned, 
are perfectly filled, but by a matter far subtler than our air, which some 
call celestial, and others aether. I shall not, I say, engage in this con- 
troversy; but thus much seems evident, that if there be such a celestial 
matter, it must make up far the greatest part of the universe known to 
us. For the interstellar part of the world, if I may so stile it, bears so 
very great a proportion to the globes, and their atmospheres too, if other 
stars have any, as well as the earth, that it is almost incomparably greater 
in respect of them, than all our atmosphere is in respect of the clouds, 
not to make the comparison between the sea and the fishes that swim in it. 

Wherefore I thought it might very well deserve a heedful inquiry, 
whether we can by sensible experiments (for I hear what has been 
attempted by speculative arguments) discover any thing about the exist- 
ence, or the qualifications of this so vast aether; and I hoped our curiosity 
might be somewhat assisted by our engine, if I could manage in it 
such a pair of bellows as I designed: for I proposed to myself to fasten 
a convenient weight to the upper basis, and clog the lower with another 
great enough to keep it horizontal and immoveable; that when by the 
help of the turning-key frequently above mentioned, the upper basis 
should be raised to its full height, the cavity of the bellows might be 
brought to its full dimensions: this done, I intended to exhaust the 
receiver, and consequently the thus opened bellows, with more than 
ordinary diligence, that so both the receiver and they might be carefully 
freed from air: after which I purposed to let go the upper base of the 
bellows, that, being hastily depressed by the incumbent weight, it 
might speedily enough fall down to the lower basis, and by so much, 
and so quickly lessening the cavity, might expel thence the matter (if 
any were) before contained in it, and that (if it could by this way be 
done) at the hole of a slender pipe fastened either near the bottom of 
the bellows, or in the upper basis; against, or over the orifice, of which 
pipe there was to be placed at a convenient distance, either a feather, 
or (if that should prove too light) the sail of a little windmill made 
of cards, or some other light body, and fit to be put into motion by 
the impulse of any matter that should be forced out of the pipe. 

By this means it seemed not improbable that some such discovery 
might be made, as would not be altogether useless in our inquiry. For 

40 CASE 1 

if, notwithstanding the absence of the air, it should appear by the effects, 
that a stream of other matter capable to set visible bodies a moving, 
should issue out at the pipe of the compressed bellows, it would also 
appear that there may be a much subtler body than common air, 13 
and as yet unobserved by the vacuists, or (their adversaries) the schools, 
that may even copiously be found in places deserted by the air; and 
that it is not safe to conclude from the absence of the air in our re- 
ceivers, and in the upper part of those tubes where the Torricellian 
experiment is made, that there is no other body left but an absolute 
vacuity, or (as the atomists call it) a vacuum coacervatum. But if, on 
the other side, there should appear no motion at all to be produced, so 
much as in the feather, it seemed that the vacuists might plausibly 
argue, that either the cavity of the bellows was absolutely empty, or else 
that it would be very difficult to prove by any sensible experiment that 
it was full; and if, by any other way of probation, it be demonstrable 
that it was replenished with aether, we, that have not yet declared for 
any party, may by our experiment be taught to have no confident ex- 
pectations of easily making it sensible by mechanical experiments; and 
may also be informed, that it is really so subtle and yielding a matter 
that does not either easily impel such light bodies as even feathers, 
or sensibly resist, as does the air itself, the motions of other bodies through 
it, and is able, without resistance, to make its passage through the pores 
of wood and leather, and also of closer bodies, which we find not that 
the air doth in its natural or wonted state penetrate. 

To illustrate this last clause, I shall add, that to make the trial more 
accurate, I waved the use of other bellows (especially not having such 
as I desired) and caused a pair of small bellows to be made with a 
bladder, as a body, which some of our former experiments have evinced 
to be of so close a texture, that air will rather break it than pass through 
it; and that the bladder might no where lose its entireness by seams, we 
glued on the two bases, the one to the bottom and the other to the oppo- 
site part of it, so that the neck came out at a hole purposely made for 
it in the upper basis; and into the neck it was easy to insert what pipe 
we thought fit, binding the neck very close to it on the outside. We had 
likewise thoughts to have another pair of tight bellows made with a very 
light clack [the valve that allows air to be drawn into the bellows] in the 
lower basis, that by hastily drawing up the other basis, when the receiver 
and bellows were very carefully exhausted, we might see by the rest, as the 
lifting up of the clack, whether the subtle matter that was expelled by the 
upper basis in its ascent would, according to the modern doctrine of the 
circle made by moving bodies, be impelled up or not. [The phrase 
"modern doctrine" refers to certain ideas of Descartes which in the middle 
of the seventeenth century were modern!] 

13 More subtle because it would not have been removed by his pump, yet not 
so subtle as to fail to be moved in a stream by a quick compression of a bellows; 
this is a very limited definition of a subtle fluid (see p. 10). 


We also thought of placing the little pipe of the bladder-bellows (if 
I may so call them) beneath the surface of water exquisitely freed from 
air, that we might see, whether upon the depression of the bellows by 
the incumbent weight, when the receiver was carefully exhausted, there 
would be any thing expelled at the pipe that would produce bubbles in 
the liquor wherein its orifice was immersed. 

To bring now our conjectures to some trial, we put into a capped 
receiver the bladder accommodated as before is mentioned; and though 
we could have wished it had been somewhat larger, because it con- 
tained but between half a pint and a pint, yet in regard it was fine and 
limber, and otherwise fit for our turn, we resolved to try how it would 
do; and to depress the upper basis of these little bellows the more easily 
and uniformly, we covered the round piece of pasteboard that made the 
upper basis with a pewter-plate (with a hole in it for the neck of the 
bladder) which nevertheless, upon trial, proved not ponderous enough, 
whereby we were obliged to assist it by laying on it a weight of lead. 
And to secure the above-mentioned feather (which had a slender and 
flexible stem, and was left broad at one end, and fastened by cement 
at the other, so as to stand with its broad end at a convenient distance 
just over the orifice of the pipe) from being blown aside to either hand, 
we made it to move in a perpendicular slit in a piece of pasteboard 
that was fastened to one part of the upper basis, as that which the 
feather was glued to was to another part. [Figure 9 is a reproduction 
of Boyle's pictures of this apparatus, the details of the arrangement of 
the feather being shown separately. Turning the key raised the top of 
the bellows; the lead weight caused it to fall when desired.] These things 
being thus provided, the pump was set a-work; and as the ambient air 
was from time to time withdrawn, so the air in the bladder expanded 
itself so strongly, as to lift up the metalline weight, and yet in part 
to sally out at the little glass-pipe of our bellows, as appeared by its 
blowing up the feather and keeping it suspended till the spring of the 
air in the bladder was too far weakened to continue to do as it had 
done. In the meantime we did now and then, by the help of a string 
fastened to the turning-key and the upper basis of the bellows, let down 
that basis a little, to observe how upon its sinking the blast against the 
feather would decrease as the receiver was further and further exhausted: 
and when we judged it to be sufficiently freed from air, we then let 
down the weight, but could not perceive that by shutting of the bellows, 
the feather was at all blown up, as it had been wont to be, though the 
upper basis were more than usually depressed: and yet it seems somewhat 
odd, that when, for curiosity, in order to a further trial, the weight was 
drawn up again, as the upper basis was raised from the lower, the sides 
of the bladder were sensibly (though not very much) pressed, or drawn 
inwards. The bellows being thus opened, we let down the upper basis 
again, but could not perceive that any blast was produced; for though 
the feather that lay just over and near the orifice of the little glass pipe 
had some motion, yet this seemed plainly to be but a shaking and almost 



vibrating motion (to the right and left hand) which it was put into by 
the upper basis, which the string kept from a smooth and uniform 
descent, but not to proceed from any blast issuing out of the cavity of 
the bladder: and for further satisfaction we caused some air to be let 
into the receiver, because there was a possibility, that unawares to us 
the slender pipe might by some accident be choaked; but though upon the 

FIG., 9. Boyle's picture of the "bladder-bellows" and feather that he used in 
trying to find a medium more subtle than air. 

return of the air into the receiver, the bases of the bellows were pressed 
closer together, yet it seemed, that, according to our expectation, some 
little air got through the pipe into the cavity of the bladder: for when 
we began to withdraw again the air we had let into the receiver, the 
bladder began to swell again, and upon our letting down the weight, to 
blow up and keep up the feather, as had been done before the receiver 
had been so well exhausted. What conjecture the opening and shutting 
of our little bellows, more than once or twice, without producing any 
blast sensible by the raising of the feather, gave some of the by-standers, 
may be easily guessed by the preamble of this experiment; but whilst I 
was endeavouring to prosecute it for my own farther information, a mis- 
chance that befel the instrument kept me from giving myself the desired 



About a junker attempt to prosecute the inquiry 
proposed in the foregoing Experiment. 

Considering with myself, that by the help of some contrivances not 
difficult, a syringe might be made to serve, as far as our present occa- 
sion required, instead of a pair of bellows; I thought it would not be 
improper to try a differing, and, in some regards, a better way to prose- 
cute an attempt which seemed to me to deserve our curiosity. 

I caused then to be made for the formerly mentioned syringe [men- 
tioned in an earlier experiment], instead of its straight pipe, a crooked 
one, whose shorter leg was parallel to the longer; and this pipe was 
for greater closeness, after it was screwed on carefully, fastened with 
cement to the barrel; and because the brass-pipe could scarce be made 
small enough, we caused a short and very slender pipe of glass to be 
put into the orifice of the shorter leg, and diligently fastened to it with 
close cement: then we caused the sucker (by the help of oil, water, 
and moving it up and down) to be made to go as smoothly as might 
be, without lessening the stanchness of the syringe. After this there 
was fastened to the handle of the rammer a weight, made in the form 
of a ring or hoop, which, by reason of its figure, might be suspended 
from the newly mentioned handle of the rammer, and hang loose on 
the outside of the cylinder, and which, both by its figure and its weight, 
might evenly and swiftly enough depress the sucker, when that being 
drawn up the weight should be let go. This syringe, thus furnished, 
was fastened to a broad and heavy pedestal, to keep it in its vertical 
posture, and to hinder it from tottering, notwithstanding the weight 
that clogged it. And besides all these things, there was taken a feather 
which was about two inches long, and of which there was left at the 
end a piece about the breadth of a man's thumb-nail (the rest on either 
side of the slender stalk, if I may so call it, being stript off) to cover 
the hole of the slender glass-pipe of the syringe; for which purpose 
the other extreme of it was so fastened with cement to the lower part of 
the syringe (or to its pedestal) that the broad end of the feather was 
placed (as the other feather was in the foregoing experiment) just over 
the little orifice of the glass, at such a convenient distance, that when 
the sucker was a little (though but very little) drawn up and let go 
again, the weight would depress it fast enough to blow up the broad 
part of the feather, as high as was permitted by the resistance of the 
stalk (and that was a good way) the spring of which would presently 
restore the whole feather to its former position. [Figure 10 shows the 
syringe with the feather, and Fig. n, the arrangement by which a 
syringe could be operated in an evacuated receiver, though in this figure 
the syringe is used to raise liquid from a small vessel.] 

All these things being done, and the handle of the rammer being 
tied to the turning-key of a capped receiver, the syringe and its pedes- 



Fig. 10. Boyle's syringe with a 
feather, used in his further search 
for a more subtle medium. 

Fig. ii. The syringe of Fig. 10 
mounted in a receiver and arranged 
to raise a liquid from a small vessel. 

Lai were inclosed in a capacious receiver (for none but such an one could 
contain them, and give scope f6r the rammer's motions) and the pump 
being set on work, we did> after some quantity of air was drawn out, 
raise the sucker a little by the help of the turning-key, and then turn- 
ing the same key the contrary way, we suffered the weight to depress 
the sucker, that we might see at what rate the feather would be blown 
up; and finding that it was impelled forcibly enough, we caused the 
pumping to be so continued that a pretty many pauses were made, dur- 
ing each of which we raised and depressed the sucker as before, and 
had the opportunity to observe, that as the receiver was more and more 
exhausted of the air, so the feather was less and less briskly driven up, 
till at length, when the receiver was well emptied, the usual elevations 
and depressions of the sucker would not blow it up at all that I could 
perceive, though they were far more frequently repeated than ever before; 
nor was I content to look needfully myself, but I made one, whom I 
had often employed about pneumatical experiments, to watch attentively, 
whilst I drew up and let down the sucker; but he affirmed that he 
could not discern the least beginning of ascension in the feather. And 
indeed to both of us it seemed that the little and inconsiderable motion 
that was sometimes (not always) to be discerned in the feather, proceeded 
not from anything that issued out of the pipe, but from some little 
shake, which it was difficult not to give the syringe and pedestal, by the 
raising and depressing of the sucker. 
And that which made our phenomenon the more considerable was, 


that the weight that carried down the sucker being still the same, and 
the motions of the turning-key being easy to be made equal at several 
times, there seemed no reason to suspect that contingencies did much 
(if at all) favor the success; but there happened a thing which did 
manifestly enough disfavor it. For I remember, that before the syringe 
w as put into the receiver, when we were trying how the weight would 
depress it, and it was thought, that though the weight were conven- 
iently shaped, yet it was a little of the least, I would not alter it, but 
foretold, that when the air in the cavity of the syringe (that now re- 
sisted the quickness of its descent, because so much air could not easily 
and nimbly get out at so small a pipe) should be exhausted with the 
other air of the receiver, the elevated sucker would fall down more easily, 
which he that was employed to manage the syringe whilst I watched 
the feather, affirmed himself afterwards to observe very evidently: so 
that when the receiver was exhausted, if there had been in the cavity 
of the syringe a matter as fit as air to make a wind of, the blast ought to 
have been greater, because the celerity that the sucker was depressed with 
was so. 

After we had long enough tried in vain to raise the feather, I ordered 
some air to be let into the receiver; and though when the admitted air 
was but very little, the motions of the sucker had scarce, if at all, any 
sensible operation upon the feather, yet when the quantity of air began 
to be somewhat considerable, the feather began to be a little moved 
upwards, and so by letting in air not all at once, but more and more 
from time to time, and by moving the sucker up and down in the in- 
tervals of those times of admission, we had the opportunity to observe, 
that as the receiver had more air in it, the feather would be more briskly 
blown up. [This experiment was devised to test Boyle's supposition 
that air at low pressure, a somewhat more subtle fluid than air at atmos- 
pheric pressure, would manifest its presence by raising the feather at 
least a little; the result bore out Boyle's expectation.] 

But not content with a single trial of an experiment of this conse- 
quence, we caused the receiver to be again exhausted, and prosecuted 
the trial with the like success as before, only this one circumstance that 
we added, for confirmation, may be fit to be here taken notice of. Having, 
after the receiver was exhausted, drawn up and let fall the sucker divers 
times ineffectually, though hitherto we had not usually raised it any 
higher at a time, than we could by one turn of the hand, both because 
we could not so conveniently raise it higher by the hand alone, and 
because we thought it unnecessary, since that height sufficed to make the 
air briskly toss up the feather; yet ex dbundanti we now took an instru- 
ment that was pretty long, and fit so to take hold on the turning-key, 
that we could easily raise the sucker between two and three inches, by 
our estimate, at a time, and nimbly depress it again; and for all this, 
which would much have increased the blast, if there had been a matter 
fit for it in the cavity of the syringe, we could not sensibly blow up the 
feather till we had let a little air into the receiver. 

46 CASE 1 

To be able to make an estimate of the quantity of air pumped out, 
or let In, when the feather was strongly or faintly, or not at all raised 
by the fall of the sucker, we took off the receiver, and conveyed a 
gage into it, but though for a while we made some use of our gage, 
yet a mischance befalling it before the operation was quite ended, I 
shall forbear to add anything concerning that trial, and proceed to say 
something of another attempt, wherein, though I foresaw and met 
with such difficulties, as kept me from doing altogether what I desired, 
yet the success being almost as good as could be expected, I shall ven- 
ture to acquaint your lordship with the trial, which was this. 

At this point Boyle describes an experiment in which the exit tube 
from his syringe was so arranged that any effluent would bubble 
through water. He found that in his exhausted receiver a syringe 
worked up and down gave no evidence that any bubbles could be 
forced through the liquid. He then continues as follows. 

I had indeed thoughts of prosecuting the inquiry by dropping from 
the top of the exhausted receiver light bodies conveniently shaped, to 
be turned around or otherwise put out of their simplest motion of de- 
scent, if they met with any resistance in their fall; and by making such 
bodies move horizontally and otherwise in the receiver, as would 
probably discover whether they were assisted by the medium. And other 
contrivances and ways I had in my thoughts, whereby to prosecute 
our enquiry; but wanting time for other experiments, I could not spare 
so much as was necessary to exhaust large receivers so diligently as such 
nice trials would exact; and therefore I resolved to desist till I had more 
leisure than I then had, or have since been master of. 

In the interim, thus much we seem to have already discovered by 
our past trials, that if when our vessels are very diligently freed from 
air, they are full of aether, that aether is such a body as will not be made 
sensibly to move a light feather by such an impulse as would make 
the air manifestly move it, not only whilst it is no thinner than com- 
mon air, but when it is very highly rarefied (which, if I mistake not, 
it was in our experiment so much, as co be brought to take up above an 
hundred times more room than before) .... 


About the falling, in the exhausted receiver, of a 

light body, fitted to have its motion visibly varied by 

a small resistance of the air. 

Partly to try, whether in the space deserted by the air, drawn out of 
our receivers, there would be any thing more fit to resist the motion of 
other light bodies through it, than in the former experiment we found 
it to impel them into motion; and partly for another purpose to be 
mentioned by and by, we made the following trials. 


We took a receiver, widely though less tail than we would have 
had, was the longest we could procure; and that we might be able, 
not so properly to let down as to let fall a body in it, we so fastened a 
small pair of tobacco-tongs to the inside of the receiver's brass-cover, 
that by moving the turning-key we might, by a string tied to one part 
of them, open the tongs, which else their own spring would keep shut. 
This being done, the next thing was to provide a body which would 
not fall down like a stone, or another dead weight through the air, 
but would, in the manner of its descent, shew, that its motion was 
somewhat resisted by the air; wherefore, that we might have a body 
that would be turned about horizontally, as it were, in its fall, we 
thought fit to join crosswise four broad and light feathers (each about 
an inch long) at their quills with a little cement, into which we also 
stuck perpendicularly a small label of paper, about an 8th of an inch 
in breadth, and somewhat more in height, by which the tongs might 
take hold of our light instrument without touching the cement, which 
else might stick to them. [Figure 12 is a reproduction of Boyle's draw- 
ing of this apparatus.] 

FIG. 12. Boyle's arrangement for allowing a feather cross to fall in an evacuated 

By the help of this small piece of paper the little instrument, of which 
it made a part, was so taken hold of by the tongs, that it hung as 
horizontal as such a thing could well be placed; and then the receiver 
being cemented on to the engine, the pump was diligently plied, till it 
appeared by a gage [here Boyle begins to use a gage, and to good 
purpose; he had previously met misfortune with this device (p. 46)] 
which had been conveyed in. that the receiver had been carefully ex* 

48 CASE 1 

hausted; lastly, our eyes being attentively fixed upon the connected 
feathers, the tongs were by the help of the turning-key opened, and the 
little instrument let fall, which, though in the air it had made some 
turns in its descent from the same height which it now fell from, yet 
now it descended like a dead weight, without being perceived by any 
of us to make so much as one turn, or a part of it: notwithstanding 
which I did, for greater security, cause the receiver to be taken off and 
put on again, after the feathers were taken hold of by the tongs; whence 
being let fall in the receiver unexhausted, they made some turns in their 
descent, as they also did being a second time let fall after the same 

But when after this, the feathers being placed as before, we repeated 
the experiment by carefully pumping out the air, neither I nor any 
of the by-standers could perceive any thing of turning in the descent 
of the feathers; and yet for further security we let them fall twice more 
in the unexhausted receiver, and found them to turn in falling as before; 
whereas when we did a third time let them fall in the well exhausted 
receiver, they fell after the same manner as they had done formerly, 
when the air, that would by its resistance have turned them around, 
was removed out of their way. 

N.B. i. Though, as I intimated above, the glass wherein this ex- 
periment was made, were nothing near so tall as I would have had it, yet 
it was taller than any of our ordinary receivers, it being in height about 
22 inches. 

2. One that had more leisure and convemency might have made a 
more commodious instrument than that we made use of; for being 
accidentally visited by that sagacious mathematician Dr. Wren, and 
speaking to him of this matter, he was pleased with great dexterity as 
well as readiness to make me a little instrument of paper, on which, 
when it was let fall, the resistance of the air had so manifest an opera- 
tion, that I should have made use of it in our experiment, had it not 
been casually lost when the ingenious maker was gone out of these 

3. Though I have but briefly related our having so ordered the 
matter that we could conveniently let fall a body in the receiver when 
very well exhausted; yet, to contrive and put in practice what was 
necessary to perform this, was not so very easy, and it would be diffi- 
cult to describe it circumstantially without very many words; for which 
reason I forbear an account that would prove too tedious to us both. . . . 


i. But here I must be so sincere as to inform your lordship, that 
this fortieth experiment seemed not to prove so much as did the fore- 
going made with the syringe; for being suspicious, that, to make the 
feathered body above mentioned turn in its fall, there would need a 
resistance not altogether inconsiderable, I caused the experiment to 
be repeated, when the receiver was, by our estimate, little or nothing 


more than half exhausted, and yet the remaining air was too far rarefied 
to make the falling body manifestly turn. 

The Annotation of the experiment just described shows Boyle in his 
tedious vein. By his own admission the experiment with the falling 
feathers is of little value, certainly of less value than the preceding 
experiments designed for essentially the same purpose. "Then why not 
omit the long description and merely summarize the result?" an im- 
patient modern reader may be inclined to exclaim. The essence of re- 
porting experimental results is to record in detail only those experiments 
that because of their outcome seem to have real significance (the results 
may be positive or negative). While admiring Boyle's candor and his 
determination to report all the details, which set the standard for sub- 
sequent investigations, one must admit that unless a greater degree of 
selection had been made by later experimenters the literature of science 
would have become impossibly burdened with irrelevant details of 
inconclusive inquiries. Many generations of experimentalists have grad- 
ually evolved an unwritten code that governs the way in which ex- 
periments are now reported. The essence of this code is accurate and 
complete recording of those experiments that the experimenter him- 
self believes to be significant; inconclusive and incomplete experiments 
need not be reported or indeed even mentioned. But in the seventeenth 
century the danger was that too little would be reported rather than too 


As has been noted, the first edition of Robert Boyle's book on 
New Experiments Physico-Mechanical Touching the Spring of the 
Air was published in 1660. Not long after, two books appeared in which 
the authors vigorously attacked both Boyle's experiments and his in- 
terpretations. One was by the famous writer on political philosophy, 
Thomas Hobbes (1588-1679), the other by an obscure supporter of the 
Aristotelian position (as interpreted by scholars of the Middle Ages) 
by the name of Franciscus Linus (1595-1675). Hobbes's position was 
that of a Plenist (see p. 26) and his arguments were based in part on 
a misunderstanding of Boyle's views and in part on the premise that 
a subtle matter existed which filled all the space. The experiments 
recorded in the preceding section deal with Boyle's attempts to obtain 
evidence for the existence of the "subtle matter" postulated by the 
Plenists. Linus's objections were directed against the whole conceptual 
scheme developed by Torricelli and Pascal, to which Boyle had made 
few additions. Probably similar objections had been expressed more 

50 CASE 1 

than once before in the decade or more in which the news o Torri- 
celli's experiment had spread and the new ideas were being discussed. 
Linus put forward the hypothesis that the space above the mercury 
column in a Torricellian tube contained an invisible membrane or cord 
which he called a funiculus. The nature of this membrane was such 
that the maximum height to which it could draw up a column of 
mercury was about 29% inches. In support of this fantastic notion 
Linus cited the well-known fact that if the upper end of the Torricel- 
lian tube is closed with a finger one seems to feel the flesh being pulled 
in. This way of performing the Torricellian experiment with a tube 
open at both ends Linus described as follows (as quoted by Boyle) : 

If you take a tube open at both ends of a good length, suppose forty 
inches long, and fill it with mercury, and place your finger on the top 
as before, taking away your lower finger, you will find the mercury to 
descend even to its wonted station [i.e., to a height of approximately 
29}^ inches], and your finger on the top to be strongly drawn within 
the tube, and to stick close unto it. Whence again it is evidently con- 
cluded that the mercury placed in its own station is not there upheld 
by the external air, but suspended by a certain internal cord [Linus's 
alleged funiculus], whose upper end being fastened to the finger, draws 
and fastens it after this manner into the tube. 

Boyle replied to this and similar arguments that the pressure of the 
outside air forced the flesh of one's finger into the top of a barometric 
tube; there was no need to assume that an invisible funiculus was 
pulling the finger down. But Boyle was always anxious to answer 
arguments by experiments. So he devised a new experiment, the results 
of which could not be explained by the aid of his adversary's hypothesis 
of a funiculus. In the course of this experiment Boyle noted the nu- 
merical relation between pressure and volume that we now call Boyle's 
Law. The discovery of an important physical law was in this instance 
rather in the nature of a by-product of Boyle's desire to bring over- 
whelming evidence to bear against a rival conceptual scheme. Contro- 
versy has often been of great importance in stimulating new advances 
in experimental science. 

Boyle's Description of his Discovery of the Relation Between Pres- 
sure and Volume. Boyle published the results of the new experiment, 
as well as lengthy arguments against both Hobbes and Linus, as an 
Appendix to the second edition of his book. This appeared in 1662. 
In Part II of this Appendix, entitled "Wherein the Adversaries Funi- 
cular Hypothesis is Examined," Boyle refers to Linus and his funiculus 
hypothesis in these words: 

The other thing, that I would have considered touching our adver- 
sary's hypothesis is, that it is needless. For whereas he denies not, that the 



air has some weight and spring, but affirms, that It is very insufficient 
to perform such great matters as the counterpoising of a mercurial cylin- 
der of 29 inches, as we teach that it may; we shall now endeavour to 
manifest by experiments purposely made [note this phrase], that the 
spring of the air is capable of doing far more than it is necessary for us 
to ascribe to it, to salve 14 the phenomena of the Torricellian experiment. 

Boyle at this point proceeds to describe how he prepared a J tube of 
glass with the short leg sealed off and the long leg open (Fig. 13). He 

kept pouring mercury into the open end until the difference in levels 
of the mercury in the two legs was 29 inches. This meant to him, as 

Mercury column T 

increased by 
pouring mercury\ 
in at T 

Shorter leg 
with scale 

Initial leve 
of mercury 

Fig. 13. Boyle's J tube, with a scale on the shorter leg reading 24 as compared 
to the initial reading of 48 (see Table i, Column A). 

it does to us, that the total pressure on the enclosed air in the short leg 
(see Fig. 13) was about twice the usual ' atmospheric pressure, and 
Boyle noted "not without delight and satisfaction*' that the volume o 
the compressed air was reduced about half. But before proceeding to 
discuss the numerical relation between pressure and volume that he 
obtained In these experiments, we may be permitted to skip to the 
conclusions that he drew from these experiments in regard to the cru- 
cial point, namely, the existence or nonexistence of Linus's funiculus. 

14 The word "solve" has been changed to "salve" (a form of "save") in agree- 
ment with the first edition (1660) of Boyle's book. 

52 CASE 1 

When the volume o the compressed air In the short arm was reduced 
to one fourth of the original volume, Boyle noted that the difference 
in levels of the mercury was a little over 88 inches. When to this is 
added the pressure of the air in terms of inches of mercury, we can 
readily see, as Boyle did, that the total pressure was 88 + 29 = 117 
inches-of-mercury as compared with 29 and a fraction, the original 
pressure. This is within an inch of being equal to four times the 
original pressure (116 inches-of-mercury). Boyle then concludes: 

It is evident, that as common air, when reduced to half its wonted 
extent, obtained near about twice as forcible a spring as it had before; 
so this thus com-prest air being further thrust into half this narrow room, 
obtained thereby a spring about as strong again as that it last had, and 
consequently four times as strong as that of the common air. And there 
is no cause to doubt, that if we had been here furnished with a greater 
quantity of quicksilver and a very strong tube, we might, by a further 
compression of the included air, have made it counterbalance the pres- 
sure of a far taller and heavier cylinder of mercury. For no man perhaps 
yet knows, how near to an infinite compression the air may be capable 
of, if the compressing force be competently- increased. [We now know 
that at room temperature some gases a^ converted to liquids if suffi- 
ciently compressed, others like those composing the atmosphere are not; 
for all gases, however, there is a temperature below which sufficient 
compression will cause liquefactkm.] So that here our adversary 
[Linus] may plainly see, that the spring of the air, which he makes so 
light of, may not only be able to /esist the weight of 29 inches, but in 
some cases of above a hundred inches [that is, including the atmospheric 
pressure] of quicksilver, and that without the assistance of his Funiculus, 
which in our present case has nothing to do. And to let you see, that 
we did not (as a little above) inconsiderately mention the weight of 
the incumbent atmospherical cylinder as a part of the weight resisted 
by the imprisoned air, we will here annex, that we took care, when 
the mercurial cylinder in the longer leg of the pipe was about an hundred 
inches high, to cause one to suck at the open orifice [T, Fig. 13]; where- 
upon (as we expected) the mercury in the tube did notably ascend. 
Which considerable phenomenon cannot be ascribed to our examiner's 
Funiculus, since by his own confession that cannot pull up the mercury, 
if the mercurial cylinder be above 29 or 30 inches of mercury. 

Here then is the point of the experiment. Linus, to explain the height 
of the mercury column in the Torricellian experiment, had to postulate 
a maximum pull of the funiculus corresponding to only 29 inches of 
mercury. Yet by combining the force of expansion of the compressed 
air in the short arm of his apparatus with the partial evacuation of the 
air above the long arm (by means of sucking with his mouth) Boyle 
is able to pull up a column of mercury whose length is several times 



29 inches. If a funiculus is involved in this (as Linus postulated), how 
can it pull up such a long column, Boyle asks. His answer follows, 

And therefore we shall render this reason of it, that the pressure of 
the incumbent air being in part taken off by its expanding itself into 
the sucker's dilated chest; the imprisoned air was thereby enabled to 
dilate itself manifestly, and repel the mercury, that comprest it, till 
there was an equality of force betwixt the strong spring of that comprest 
air on the one part, and the tall mercurial cylinder, together with the 
contiguous dilated air, on the other part. 

'Numerical Relation of Pressure and Volume. Boyle's method of 
measuring volume was crude; it consisted of measuring the distance 
between the top of the sealed off shorter leg and the mercury level in 
the same leg. Clearly this measurement of a distance is a true measure 
of the volume only if the tube is of uniform diameter, which would be 
true only approximately. A paper scale divided into inches and frac- 
tions was pasted on the outside of the shorter leg and a similar but 
longer scale on the outside of the longer leg. The position of the two 
mercury levels could then be noted and the difference in pressure re- 
corded. The results were given by Boyle in a table which is reproduced 
in Table i. 

TABLE i. Compression of air (Boyle's original data). 



C D 




29 %e 


A. The number of equal spaces in the 


01 7 Ae 

30 9ie 

30 %s 

shorter leg, that contained the same 


02 % 

31 *%6 

31 X %6 

parcel of air diversely extended. 



33 % 




35 %a 



07 Ufa 


36 15 /i9 

B. The height of the mercurial cylin- 


10 %6 

39 %e 

38 7 ^ 

der in the longer leg, that com- 


12 %6 

41 *9ie 

41 %7 

pressed the air into those dimen- 


15 %6 

44 %6 

43 Hi 



17 ^is 

.3 47 Vis 




S 50 %s 


C. The height of the mercurial cylinder 


25 %e 

^ 54 % 

53 i9is 

that counterbalanced the pressure of 


29 Hie 

04 58 % 


the atmosphere. 



2 61 %e 

60 1 %s 


34 %J 

-g ^4 Vi 



37 %* 

? 67Vie 


D. The aggregate of the two last col- 



< 70 x Vi6 


umns B and C, exhibiting the pres- 



74 %6 

73 x Vi9 

sure sustained by the included air. 


48 x %e 

77 ^ifi 



53 % 

82 % 

82 *lr 


58 %e 

87 ^16 


E. What that pressure should be ac- 


63 % 



cording to the hypothesis, that sup- 


71 %6 

100 7 /ie 


poses the pressures and expansions 


78 *%e 

107 !%e 

107 7 /is 

to be in reciprocal proportion. 


88 7 /is 


116 % 

54 CASE I 

As to the origin of the hypothesis that pressure and volume are recip- 
rocally related, Boyle has this to say: 

I shall readily acknowledge, that I had not reduced the trials I had 
made about measuring the expansion of the air to any certain hypothesis, 
when that ingenious gentleman Mr. Richard Townley was pleased to 
inform me, that having by the perusal of my physico-mechanical experi- 
ments been satisfied that the spring of the air was the cause of it, he 
endeavoured (and I wish in such attempts other ingenious men would 
follow his example) to supply what I had omitted concerning the re- 
ducing to a precise estimate, how much air dilated of itself loses of its 
elastical force, according to the measures of its dilatation. [Boyle in his 
book had tried without success to reduce to numerical terms the effec- 
tiveness of his engine in terms of the ratio of the volumes of the cylinder 
and the receiver. One of his readers seems to have grasped the point 
that probably pressure and volume were inversely proportional to each 
other.] He added, that he had begun to set down what occurred to him 
to this purpose in a short discourse, whereof he afterwards did me the 
favour to shew me the beginning, which gives me a just curiosity to 
see it perfected. But, because I neither know, nor (by reason of the 
great distance betwixt our places of residence) have at present the op- 
portunity to inquire, whether he will think fit to annex his discourse 
to our appendix, or to publish it by itself, or at all; and because he hath 
not yet, for aught I know, met with fit glasses to make an any-thing- 
accurate table of the decrement of the force of the dilated air; our 
present design invites us to present the reader with that which follows, 
wherein I had the assistance of the same person, that I took notice of 
in the former chapter, as having written something about rarefaction 
[this appears to refer to Hooke]: whom I the rather make mention of 
on this occasion, because when he first heard me speak of Mr. Townley s 
suppositions about the proportion, wherein air loses of its spring by dila- 
tation, he told me he had the year before (and not long after the pub- 
lication of my pneumatical treatise) made observations to the same 
purpose, which he acknowledged to agree well enough with Mr. 
Townley' s theory: and so did (as their author was pleased to tell me) 
some trials made about the same time by that noble virtuoso and emi- 
nent mathematician the Lord Brounc\er, from whose further enquiries 
into this matter, if his occasions will allow him to make them, the 
curious may well hope for something very accurate. 

It is interesting that at least three of Boyle's contemporaries suggested 
the relation that we now know as Boyle's law as a result of reading 
about Boyle's difficulties in calculating the effectiveness of his engine. 
Boyle obviously became so interested in the numerical relation be- 
tween pressure and volume that his initial objective, namely, to raise 
a column of mercury more than 29 inches by suction, i's rather lost 
sight o Certainly in the presentation of all this material, his adver- 


sary's point of view is brought in rather casually, though he does finally 
conclude with the statement, 

I suppose we have already said enough to shew what was intended: 
namely, that to salve the phenomena there is not of our adversary's 
hypothesis [i.e., the funiculus] any need: the evincing of which will 
appear to be of no small moment in our present controversy to him that 
considers, that the two main things, that induced the learned examiner 
to reject our hypothesis, are, that nature abhors a vacuum; and that 
though the air have some weight and spring, yet, these are insufficient 
to make out the known phenomena; for which we must therefore have 
recourse to his Funiculus. Now as we have formerly seen, that he has 
not so satisfactorily disproved as resolutely rejected a vacuum, so we 
have now manifested, that the spring of the air may suffice to perform 
greater things than what our explication of the Torricellian experiments 
and those of our engine obliges us to ascribe to it. Wherefore since 
besides the several difficulties, that incumber the hypothesis we oppose, 
and especially its being scarce, if at all, intelligible, we can add that it 
is unnecessary; we dare expect, that such readers as are not biassed by 
their reverence for Aristotle, or the Peripatetick schools, will hardly reject 
an hypothesis, which, besides that it is very intelligible, is now proved 
to be sufficient, only to imbrace a doctrine, that supposes such a rare- 
faction and condensation, as many famous Naturalists rejected for its 
not being comprehensible, even when they knew of no other way 
(that was probable) of salving the phenomena wont to be explicated 
by it. 

In this same chapter Boyle describes some experiments on what he 
calls the "debilitated force of expanded air.** This amounts to another 
way of measuring the relation between volume and pressure. In this 
case the original sample of air is not compressed but expanded by di- 
minishing the pressure. This Boyle accomplished very simply by en- 
closing a sample of air in a long thin tube closed at the upper end and 
immersed for several feet in a long tube of mercury. When the inner 
tube is raised, the contained air is allowed to expand, a suitable scale 
serving to measure the change in volume (assuming uniform bore) 
and the diminished pressure. (This experiment can be conveniently 
performed today by using an inverted glass burette for the inner tube 
and a tall glass cylinder to contain the mercury.) 

Boyle makes no explicit statement about the effect of temperature 
on the accuracy of his results. He was quite aware, however, of the 
fact that air expands^on heating and contracts on cooling. He was curi- 
ous to see whether the air compressed to a quarter of its volume be- 
haved in this respect like air under atmospheric pressure. He therefore 
warmed the short leg of his bent tube with a candle and cooled it with 
water, noting in qualitative terms the changes of volume that occurred. 

56 CASE 1 

They were not large. This fact must have assured Boyle that the minor 
fluctuations in the room temperature during the experiment in which 
he varied the height of the column of mercury would not affect the 
significance of his results. We now know that the pressure of a given 
volume of gas increases by about %so of its value at room temperature 
for every (Fahrenheit) degree increase in temperature. Therefore, an 
increase of as much as five degrees during Boyle's experiment would 
have introduced an error of only about %so or a little less than %oo, 
which is about the difference between the observed and calculated 
pressures (Columns D and E, Table i) in the extreme case. 

Today, no one would think of measuring the relation between pres- 
sure and volume of a gas with any pretense to accuracy unless the 
temperature were controlled. Careful experiments have shown that 
even at constant temperature Boyle's law, 

Pressure X Volume = constant, 

is only approximately true for gases at atmospheric pressure. The de- 
viations from Boyle's law (the change in the product of volume and 
pressure as pressure increases) are greater the greater is the pressure 
for a given gas; the gases that are not far from the point of conden- 
sation deviate widely from Boyle's law. 

An interesting comparison can be made between Boyle's law and 
the relation between pressure in a liquid and depth below the surface. 
The first is based on experimental findings and is only approximate; 
the second appears to be a consequence of definitions and was pre- 
sented in the sixteenth century as a deduction from self-evident prop- 
ositions in a manner reminiscent of geometry. The hydrostatic principle 
here involved may be expressed by a "law" in the form P (pressure in 
the liquid) = D (depth) + A (atmospheric pressure), if appropriate 
units are taken. On analysis, it becomes evident that this is true only if 
the change of density of the liquid with pressure can be neglected (it 
can be for all practical purposes for considerable depths of water). Con- 
stant temperature throughout the liquid must be assumed (just as 
Boyle's law is true only for constant temperature). The deviations from 
Boyle's law decrease with decreasing pressure, and for very attenuated 
gases the observed relations between pressure and volume follow Boyle's 
law closely. To the extent that the hydrostatic law defines an ideal 
liquid, it may be comparable with Boyle's law as a definition of an 
ideal gas. 

Boyle's formulation of the relation between two variables, volume 


and pressure of a gas, is typical of a vast amount of scientific infor- 
mation that began to be accumulated about the middle of the seven- 
teenth century. In the case at hand, this information was obtained in- 
cidentally to a controversy about the Torricellian conceptual scheme 
as extended by Boyle. As scientific experimentation continued, how- 
ever, the aim of the investigator was often more directly to obtain 
quantitative data about the relation between two variables, one of 
which was said to be a function of the other. The realization of what 
were the significant variables was usually closely connected with the 
development of new concepts or conceptual schemes (theories). But 
the experimental difficulties of controlling or measuring the other vari- 
ables were often considerable. The recognition of the variable factors 
in a changing situation and the development of methods of measuring 
these factors often constitute a major advance in science. 

The concept that air was compressible did not originate with Boyle. 
Torricelli, in his letter of June 28, 1644 describing his first experiments, 
in explaining what he means by the pressure of the atmosphere uses 
the analogy of a cylinder of wool (easily compressible by hand), and 
there had been earlier discussions of the compressibility of air. On the 
other hand, Pascal, in his treatise written in 1648 (published in 1663), 
makes little reference to the vast difference in compressibility between 
water and air. He makes use of the analogy between hydrostatic pressure 
and air pressure but treats air for the most part as though it were water 
of very low density. One can say that Boyle extended Torricelli's con- 
ceptual scheme by emphasizing the "spring of the air." He was led 
to do so because the operation of von Guericke's pump depends on the 
fact that air expands and contracts with changing pressure almost 
instantaneously and to a very large extent; one can "feel" the spring of 
the air when one operates an air pump! 

Boyle noted in his first book that there were at least two ways of 
imagining the composition of air to account for its great compressibil- 
ity. One was to think of the particles as each being compressible like 
a spring or a bit of wool. One can conceive of the air, wrote Boyle, as 
"a heap of little bodies, lying one upon another, as may be resembled to 
a fleece of wool." The other way was to think of the particles as whirled 
around in the subtle fluid postulated by Descartes as filling all space. 
According to this latter view, Boyle said, "it imports very little, whether 
the particles of the air have the structure requisite to springs, or be of 
any other form (how irregular soever) since their elastical power is not 
made to depend upon their shape or structure, but upon the vehement 

Boyle declares he is not willing "to declare peremptorily for either of 
them [i.e., the ideas] against the other." He goes on to say, "I shall 

58 CASE 1 

decline meddling with a subject, which is much more hard to be expli- 
cated than necessary to be so by him, whose business it is not, in this 
letter, to assign the adequate cause of the spring of the air ? but only to 
manifest, that the air hath a spring, and to relate some of its effects." 

Boyle was an adherent of what is sometimes called the corpuscular 
philosophy a point of view that derives from one branch of ancient 
Greek thought. One could speculate and argue whether matter could 
be divided and subdivided indefinitely or whether there were ultimate 
particles, often called atoms. Either of the "explanations" put forward 
by Boyle for the "spring of the air" was in harmony with the atomistic 
idea of the structure of matter. Though reserving the right in his first 
account of the subject to experiment later to test the alternative con- 
cepts, he seems to have done so only indirectly by searching for Des- 
cartes' subtle fluid. When speculation about the nature of gases became 
important for the advance of chemistry at the end of the eighteenth 
century, the picture of a gas then in favor was that of contiguous but 
easily compressible particles filling the space. This atomic picture was 
still a speculative idea, however, hardly a working hypothesis, until 
Dalton used it to relate the constant ratio by weights of elements in 
compounds. The distinction between a general speculative idea, a 
working hypothesis on a grand scale, and a new conceptual scheme is 
well illustrated by comparing the history, in the seventeenth century, 
of the notion of matter being composed of atoms with that of the 
idea of a sea of air surrounding the earth. The first remained a specu- 
lative idea throughout the period; the second soon emerged as a new 
conceptual scheme which by 1700 was almost universally accepted. 
It was not until Dalton in 1805 put forward his "atomic theory" (cer- 
tainly at first only a working hypothesis on a grand scale) that from 
the general speculative idea one could draw deductions that could be 
tested by experiment (Case 4 of this series). 

At what point in history the conceptual scheme about air and air 
pressure became a "fact" and whether or not the atomic nature of 
matter is now a "fact" can be left for the reader to debate. If one 
adopts a cautious attitude about science, one will reserve the use of 
the word "fact" to designate reproducible observations (at least when 
one is attempting to speak carefully about science). The word "theory" 
is commonly used to mean either a working hypothesis or a well- 
accepted conceptual scheme. Because of the resulting ambiguities, we 
prefer to use the phrases "working hypothesis on a grand scale" or 
"broad working hypothesis" for a new idea in its initial phases. As soon 
as the deductions from such a hypothesis have been confirmed by 
experimental test and the hypothesis is accepted by several scientists, it 
is convenient to speak of it as a conceptual scheme. In a cautious rnood 


one retains the phrase no matter how certain one may feel about the 
postulates. The reader need hardly be reminded that in 1950 the ideas 
about the structure of the nucleus of the atom are in a state where 
working hypotheses on a grand scale are in the process of becoming 
conceptual schemes (or if one must use the word, new theories!). 


The Two Traditions. As was pointed out in the Foreword, the 
development of experimental science in the seventeenth century was the 
consequence of the combination of deductive reasoning with the cut- 
and-try type of experimentation. Two great figures of this period who 
contributed to the study of pneumatics symbolize the two traditions 
whose combination produced modern science. Blaise Pascal was pri- 
marily a mathematician, Robert Boyle primarily an experimentalist. 
A study of their writings illustrates the two streams of thought and 
action that were found in the seventeenth century. In Pascal's treatise 
on hydrostatics and his work on pneumatics it is hard to tell whether or 
not most of the so-called experiments were ever performed. They may 
well have been intended rather as pedagogic devices as demonstra- 
tions that the reader performs in his imagination in order better to 
understand the principles expounded. The argument is by deductive 
reasoning from a few postulates; here and there a check by actual ex- 
periment, as the case of the Puy-de-D6me observations, may be of great 
significance. Yet it will be recalled that one may question whether 
Pascal's collaborator, Perier, was an accurate reporter; it seems probable 
that, convinced of the general effect he was looking for, namely, the 
change of barometric reading with height, he could not resist the temp- 
tation to give results with such an accuracy as to carry conviction to those 
steeped in the tradition of mathematical reasoning (see pp. 8 and 28). 
Boyle in one of his discussions of hydrostatics (1666) gently pokes 
fun at Pascal for having written of experiments that appeared im- 
possible of execution. Pascal, said Boyle, does not state that he actually 
tried the experiments; "he might possibly have set them down as 
things that must happen, upon a just confidence that he was not mis- 
taken in his ratiocinations." He further chides Pascal for not giving 
sufficient details that anyone can repeat his experiments (if he ever 
really did them). Boyle was on solid ground here, for, as we have 
seen, he was if anything overconscientious in recording all possible 
information that might be of assistance to another investigator. As an 
example of some of the things Pascal described that strained one's 
credulity, Boyle refers to an experiment in which a man sits 20 feet 

60 CASE I 

under water and places against his thigh a tube that extends above the 
surface of the water. But, writes Boyle, Pascal "neither teaches us how 
a man shall be enabled to continue under water, nor how, in a great 
cistern full of water 20 feet deep, the experimenter shall be able to 
discern the alterations. . ." 

One can trace through the history of physics and chemistry the two 
traditions represented by Pascal and Boyle, though sometimes both 
appear to be almost equally represented in the work of a single man, 
as in the cases of Galileo, Newton, and perhaps Lavoisier. In the 
twentieth century one thinks of the names of Einstein and Lord Ruth- 
erford, one a mathematician, the other an experimentalist, each rep- 
resenting by his revolutionary work the best in the two approaches 
that together made modern science. 

Science and the Practical Arts. The study of pneumatics may have 
started as the result of an interest by a professor in the practical art 
of pumping water. Galileo, 15 in his Dialogues Concerning Two New 
Sciences, published in 1638, places in the scientific record for the first 
time what must have been a well-known fact to those who built and 
operated pumps, namely, that water will not rise in a lift pump above 
about 34 feet. One of the characters in the dialogues says, "I once saw a 
cistern which had been provided with a pump under the mistaken 
impression that the water might thus be drawn with less effort or in 
greater quantity than by means of the ordinary bucket. , . This pump 
worked perfectly so long as the water in the cistern stood above a 
certain level; but below this level the pump failed to work. When I 
first noticed this phenomenon I thought the machine was out of order; 
but the workman whom I called in to repair it told me the defect was 
not in the pump but in the water, which had fallen too low to be 
raised through such a height; and he added that it was not possible, 
either by a pump or by any other machine wording on the principle 
of attraction, to lift water a hair's breadth above eighteen cubits'" 

The words that we have italicized convey important historical in- 
formation. It seems quite clear that Galileo's interest in a scientific 
problem had arisen from the observation of a practical art, namely, 
pumping water; furthermore, it seems evident that the knowledge 
about the limitations of a lift pump was common among the workmen. 
Indeed, illustrations from books of the sixteenth century show tandem 
pumps (one above the other) lifting water from mines. It is interesting 
that while Galileo himself made little or no contribution to the solu- 

15 Galileo Galilei (1564-1642), regarded by many as the real founder of modern 
science; certainly the greatest single figure in physical science after Archimedes 
and before Newton; a professor at the universities of Pisa and Padua and later 
resident at the court of the Grand Duke of Florence. 


tion of the scientific problem of relating the limitation of a water 
pump to other phenomena, his pupil Torricelli did. 

Although pneumatics in origin was thus closely related to a prac- 
tical art (and pumps with their various parts valves, cylinders, 
plungers recur throughout the story), the advance in science did 
not change the art of pumping water at least not in the seventeenth 
century. There is no evidence, indeed, that "any of Boyle's work had 
immediate consequences of practical value. Even in scientific work 
his devices for collecting gases in vacuo and transferring them under 
pressure to an evacuated vessel were scarcely employed by chemists 
until the twentieth century. An alternative procedure the use of the 
pneumatic trough which was invented somewhat later than Boyle's 
time, was found to be preferable. A study of the work of the "pneumatic 
chemists" of the late eighteenth century (Case 2 of this series) shows 
how little was the influence of the techniques for handling gases worked 
out by Boyle and Papin. 

The failure of the scientific world to use vacuum pumps in the 
eighteenth century is readily explained by anyone who has had ex- 
perience with evacuated systems. Boyle's pumps were expensive and 
difficult to operate, and before glass blowing and metal working had 
reached a high state of development, it was almost impossible to in- 
sure against leaks. It was only in the second half of the nineteenth 
century that distillations at pressures of an inch of mercury carne into 
common practice. The development of the incandescent light which 
originally required a high vacuum (pressure of io~ 3 mm-of-mercury or 
less) stimulated the improvement of vacuum pumps for industrial 
purposes. New types of pumps together with chemical procedures now 
make it possible to evacuate large vessels to a pressure as low as 
io"~ 5 mm-of-mercury; indeed, pressures as low as io~ 10 mm-of-mercury 
have been reported. 

Denis Papin (1647-1712) was Boyle's collaborator in his later work 
in pneumatics. He was the inventor of the pressure cooker (originally 
called Papin's digester) which has only in the middle of the twentieth 
century come into its own as a device useful to the housewife. This 
invention was closely related to Boyle's studies of the behavior of ma- 
terials not only in vacuo but in compressed air. John Evelyn, in his 
famous diary under date of April 15, 1682, records with appreciation 
that the members of the Royal Society partook of a supper cooked in 
a digester. He remarks, "This philosophical supper caused much mirth 
amongst us and exceedingly pleased all the company." The fact that 
Papin later made several designs for steam engines serves to connect 
Boyle's work with the practical developments of the eighteenth 

62 CASE 1 

Newcomen's atmospheric engine (1712) can be thought of as a 
practical outcome of the work of the investigators of pneumatics in 
the seventeenth century. But the connection is far from direct. By the 
end of the seventeenth century, the Torricellian scheme was accepted 
as a matter of course. So, too, was the concept of air as an elastic 
fluid, and the connection between water and steam was beginning to 
be understood. Therefore, while no direct applications of the new 
discoveries in pneumatics to the practical arts can be traced in the 
seventeenth century, it is clear that all scientists and inventors who 
were concerned with gases or vapors were from Boyle's time on 
thinking in terms of the new concepts and Torricelli's conceptual 
scheme. In the seventeenth and eighteenth centuries, advances in 
science and progress in the practical arts by continued empirical ex- 
perimentation were two parallel activities. The scientists and inventors 
were in communication and shared the same ideas, but it was not 
until the nineteenth century that the concepts of science and the ac- 
cumulated scientific information became of major importance to the 
practical men of industry and commerce. And only in the twentieth 
century have the two activities science and the practical arts be- 
come intimately associated in almost every industrial activity. 

Science and Society. The casual way in which Robert Boyle refers 
to the work of other investigators is worthy of special notice. So in- 
complete are his references that we cannot tell today how much of 
his work in pneumatics was original. This disorganized state of scien- 
tific communications is typical of the first half of the seventeenth 
century. When the new experimental philosophy was beginning to 
attract attention, news of scientific discoveries usually circulated by 
means of letters between learned men. The publication of scientific 
books was sporadic and often greatly delayed. The need for some 
regular method of recording short notices about scientific experiments 
led to the establishment of scientific journals in the second half of the 
century. The formation of scientific societies was of great significance 
in this connection since they sponsored scientific journals which, in 
the case of the Transactions of the Royal Society (London) and the 
Memoires of the French Academy (Paris), have continued almost 
without interruption to the present day. For those students who are 
interested in either the political ferment in England of the seventeenth 
century or the connection between the development of literature and 
philosophic thought, a study of the founding of the Royal Society will 
be rewarding. The books listed below in the first section are recom- 
mended as a basis for a consideration of the interaction of science 
and society in this period. 



1. A Bibliography of the Honourable Robert Boyle, by J. F. Fulton 

(Oxford University Press, Oxford, 1932). 

2. Science and Society 

The Life and Worlds of the Honourable Robert Boyle, by Louis Tren- 
chard More (Oxford University Press, New York, 1944). The first 113 pages 
are recommended; with the author's evaluation of Robert Boyle's work in 
chemistry the editor of this Case cannot agree, 

Scientists and Amateurs: A History of the Royal Society, by Dorothy 
Stimson (H. Schuman, New York, 1948). 

The Role of Scientific Societies in the Seventeenth Century, by Martha 
Ornstein (University of Chicago Press, Chicago, ed. 3, 1938). 

The Seventeenth Century Background, by Basil Willey (Columbia Uni- 
versity Press, New York, 1942), is to be especially recommended for students 
interested in literature as collateral reacling. The first three chapters present 
an interesting view of the impact of Bacon's ideas and Galileo's work. 

3. Supplementary Reading to the Case History 

The Physical Treatises of Pascal. The Equilibrium of Liquids and the 
Weight of the Mass of the Air [by Blaise Pascal], translated by I. H. B. 
and A. G. H. Spiers, with introduction and notes by Frederick Barry 
(Columbia University Press, New York, 1937). 

This little volume, containing all of Pascal's "brief but brilliantly in- 
genious labors in natural science, together with the remarkably well-executed 
investigations of Perier which completed them, was put together by Perier 
and published at Paris in 1663, a year after Pascal's death." Since the text 
.translated includes a summary of Boyle's early work on pneumatics, and 
since this Columbia edition furthermore contains translations of relevant 
passages from the writings of Stevin, Galileo, and Torricelli, the volume 
is a useful one indeed. Information about the influence of Hero of Alexan- 
dria's Pneumatica is given in an article by Marie Boas in Isis, vol. 40 (1949), 

P . 3 8. 

The Science of Mechanics, by Ernst Mach (first German edition, 1883; 
last major revisions, 1911; English translation by T. J. McCormack, Open 
Court Publishing Co., Chicago, 1893; current (1942) edition considerably 
rearranged). For hydrostatics and pneumatics, see especially chap, i, sees, vi 
and vii and chap, iii, sec. x. 

This historical and critical survey of mechanics ha.s become a landmark 
in the development of the logical analysis of science. Although it contains 
a wealth of useful facts and penetrating critiques, some caution is needed 
in using it today. The historical research available to Mach was both 
limited and biased in such a way that he inevitably tended to overemphasize 
the contributions of certain individuals. 


The Overthrow of the 
Phlogiston Theory 

The Chemical Revolution 





The overthrow of the phlogiston theory involved the develop- 
ment of a superior conceptual scheme. There can be no doubt that the 
author of the new ideas was the French chemist Lavoisier, often re- 
ferred to as the "father of modern chemistry." The chemical revolution 
did not occur overnight, however, and Lavoisier did not accomplish 
his results singlehanded. By studying the evolution of a new conceptual 
scheme we can see the difficulties with which pioneers in science almost 
always have to contend, and the false steps that usually accompany 
even the most successful forward marches. We likewise see how, by 
the end of the eighteenth century, science had become an organized 
activity with its own methods of making public new results. As com- 
pared with the first half of the seventeenth century, the interchange 
between leading investigators was prompt and effective. As compared 
with our own time, or even with the middle of the nineteenth century, 
however, the publication of results was sporadic and incomplete. For 
example, although the English experimenters Priestley and Cavendish 
could read of Lavoisier's work soon after it was completed (and vice 
versa), the fact that the Swedish chemist Scheele had prepared pure 
oxygen gas and studied its properties remained unknown to what was 
then the "scientific world" for several years. Scheele's experiments were 
completed before 1773. His characterization of a new gas which he 
called "fire air" was quite unambiguous. The manuscript of his book 
on Air and Fire describing these discoveries and interpreting them 
was not delivered to the printer before 1775 and not published until 
1777. This delay prevented his discovery of oxygen, which antedated 
Priestley's, from being the effective discovery that influenced the work 
of other men. 

The chemical revolution may be conveniently thought of as occur- 
ring in the following stages: 

68 CASE 2 

(1) Lavoisier's experiments with sulfur and phosphorus in 1772 in 
which he noted a "prodigious quantity of air was fixed.' 5 

(2) The effective discovery of oxygen, the unraveling of its relation 
to the calcination of metals in air, and its role in the respiration 
of animals, 1774-1778. 

(3) The determination of the composition of water, 17821783. 

(4) The extension and precise formulation of the new conceptual 
scheme in terms of a new chemical nomenclature in Lavoisier's 
Traite ~lementaire de Chimie, 1789. 

In this Case we shall center our attention on the second of these 
stages. In many ways this is the most interesting part of the entire 
story, for one can trace here the stumbling way in which two great 
scientists Joseph Priestley (1733-1804) the English nonconformist 
clergyman, and Antoine Lavoisier (1743-1794) of Paris proceeded 
through the jungle of new experimental facts. One can see how the 
publications of the two men influenced the course of scientific history. 
In the case of Lavoisier we can follow his line of reasoning and see his 
errors particularly clearly because of the way in which his most im 
portant single paper was given to the world. On the threshold of suo 
cess, he is diverted by a faulty interpretation of an experiment and 
recovers his sense of direction only after some months of labor and 
with the assistance of the English chemist. We are here permitted to 
follow the course of a revolutionary scientific discovery in much the 
same fashion as a slow-motion picture of a critical moment enables us 
to understand what happened in a football game. 

The chemical transformations involved in this case are few, and in 
the light of modern chemistry they are relatively simple. It will assist 
the student of this example of "science in the making" to master first 
a few chemical facts as they are expressed in terms of the conceptual 
scheme that has been the gospel of chemists since Lavoisier's final 

Air is primarily a mixture of two gases, oxygen and nitrogen. Com- 
bustion and respiration involve chemical reactions between carbon 
compounds and oxygen; the products of these reactions are water and 
carbon dioxide, except in the case of charcoal, when carbon dioxide 
alone is formed. When a metal is heated in air, it forms an oxide by 
combining with the oxygen; the product was known to the early 
chemists as a "calx" and the process as "calcination." When many 
oxides of metals are heated with charcoal, the oxygen combines with 
the charcoal forming carbon dioxide ("fixed air" to the chemists of the 
eighteenth century) and the metal. Mercury oxide, a red powder, also 
known as red precipitate or mercurius calcinatus per se f has the un- 



usual property of being converted into the metal mercury and oxygen 
when heated quite hot without charcoal. Therefore, one can start with 
mercury metal and obtain the oxide by heating the metal in air, and 
then by heating the oxide still hotter, regenerate the mercury. If one 
arranges to collect the gas evolved in this last process, one will have 
oxygen gas at one's disposal. The three reactions with which Lavoisier 
and Priestley were concerned were: 






2 HgO 

oxide of 


(red powder) 

Decomposition of oxide 


very hot 

2HgO > 

oxide of yields 


Reduction with addition 
of charcoal (also called 
reduction with phlogiston!) 





oxide of 








CO 2 

or "fixed 


The Phlogiston Theory. A few words about the phlogiston theory 
are necessary by way of introduction. Joseph Priestley never gave up 
his belief in the theory, In his last book, published in 1796, he wrote, 
"There have been few, if any, revolutions in science so great, so sudden, 
and so general, as the prevalence of what is now usually termed the new 
system of chemistry, or that of the ^/phlogistons, over the doctrine of 
Stahl, which was at one time thought to have been the greatest discov- 
ery that had ever been made in the science. I remember hearing Mr. 
Peter Woulfe, 1 whose knowledge of chemistry will not be questioned, 
say, that there had hardly been any thing that deserved to be called a 
discovery subsequent to it. Though there had been some who occa- 
sionally expressed doubts of the existence of such a principle as that of 

Chemist and mineralogist, born 1727, died 1803, resident of London and 
Paris, member of the Royal Society from 1767. 

70 CASE 2 

phlogiston, nothing had been advanced that could have laid the foun- 
dation of another system before the labors of Mr. Lavoisier and his 
friends, from whom this new system is often called that of the 

The significance of this quotation lies in the admission by Priestley s 
the die-hard upholder of the phlogiston theory, that Lavoisier and his 
friends had brought about a chemical revolution. Although still raising 
doubts about the new views and retaining the vocabulary of the 
phlogiston theory, Priestley in this last publication seems to be ad- 
mitting that he is fighting a rear-guard action. His statement as to 
the former high position held by StahTs doctrine of phlogiston is con- 
firmed by the writings of many eighteenth-century scientists. The 
phlogiston theory was a broad conceptual scheme into which could be 
fitted most of the chemical phenomena of the mid-eighteenth century. 
The lineage of this theory can be traced back to the alchemists. (It 
should be noted that a metal, according to this theory, is more complex 
than is the corresponding oxide.) In particular, it accounted for one of 
the simplest chemical processes then employed for practical ends, 
namely, the preparation of metals from their ores. The transformation 
of an earthy substance into a metal in the smelting process appeared to 
be much the same whether the metal was iron, or tin, or copper. What 
could be more plausible than to assume that in each instance the ore, 
when heated with charcoal, took up a "metallizing principle*' which 
conferred upon the earth the properties of a metal? If one called this 
hypothetical substance phlogiston, an "explanation" for metallurgy was 
at hand: 

Metallic ore + Phlogiston Metal 

(an oxide) from 


The fact that charcoal would burn by itself when heated indicated to 
the founders of the phlogiston theory that the phlogiston escaped in 
the process and became combined with the air. In general, substances 
that burned in air were said to be rich in phlogiston; the fact that 
combustion soon ceased in an enclosed space was taken as clear-cut 
evidence that air had the capacity to absorb only a definite amount of 
phlogiston. When air had become completely phlogisticated it would 
no longer serve to support combustion of any material, nor would a 
metal heated in it yield a calx; nor could phlogisticated air support 
life, for the role of air in respiration was to remove the phlogiston from 
the body. Everything fitted together very well. 

The phlogiston theory was almost universally accepted at the time 
of the American Revolution and was the basis of the chemistry then 


taught to college students as part of their instruction in natural philos- 
ophy. The lecture notes of Professor Samuel Williams, the Hollis 
Professor of Mathematics and Natural Philosophy, 1780-1788, at Har- 
vard illustrate the convincing way in which the phlogiston theory 
could be presented to a class. Presenting the subject of Pneumatics, 
Professor Williams listed six different airs, and about common or 
atmospherical air had this to say: 

"Among the various kinds of permanently elastic Fluids we may 
begin with Common or Atmospherical Air. Atmospherical Air is that 
which we breathe, with which we are constantly surrounded, and 
which is common to every country and place. And with regard to this 
kind of Air several observations may be made. Thus: Common or 
atmospherical Air may combine, or be charged with many sub- 
stances. Thus water is held in solution by Air, and Rain, Snow, and 
Hail appear to be precipitations from it. ... But what is worthy of 
a particular observation, common or atmospherical Air is generally 
charged with a large quantity of Fire or Phlogiston. The Chemists 
sometimes speak of Fire and Phlogiston as being the same thing, or 
signifying the same element. But we are not absolutely certain that 
this is the case. By Phlogiston we mean no more than the principle 
of Inflammability; or that by which bodies become combustible or 
capable of burning. And that there is such a principle or element as 
Phlogiston, and that common Air may be charged with large quanti- 
ties of it may be easily represented. 

"Example: Take some combustible substance and let it be inflamed 
or set on fire: In this state inclose it in a vessel containing a small 
quantity of atmospherical air. Effect. The combustion will continue 
but a small time and then cease. Part of the combustible substance is 
reduced to ashes and the other part remains entire. And the Air ap- 
pears to be changed and altered . . . Here then we have a representation 
of what the chemists call Phlogiston and of the Air's being loaded with 
it. In the confined air the combustible matter continues burning until the 
air becomes loaded with something that prevents any further combus- 
tion. And being confined by the closeness of the vessel whatever the 
matter be with which the air is loaded it is confined within the vessel 
and cannot escape. . . . 

"It seems therefore from this Experiment that Phlogiston must be a 
real Substance, and that the Air is loaded or saturated with it. For 
what can the enclosing the combustible matter in the Phial do but to 
prevent the escape or dispersion of some real substance? And is it 
not evident that so long as the air can receive this substance from the 
combustible matter so long the body will continue burning; and that as 
soon as the Air is saturated and can receive no more of the Phlogiston, 

72 CASE 2 

the combustion must cease for no more Phlogiston can escape or be 
thrown out from the burning body. And therefore when fresh air is 
admitted to receive Phlogiston, the combustion will again take place. 
And hence are derived the phrases of phlogisticated and dephlogis* 
ticated air. By phlogisticated air is intended air which is charged or 
loaded with Phlogiston, and by dephlogisticated air is meant Air which 
is free from Phlogiston; or which does not contain this principle or 
element of inflammability." 

Qualitatively, the phlogiston theory was a satisfactory framework to 
accommodate the chemical phenomena known in the 1770*5. Even 
some quantitative changes could be accounted for as explained by 
Professor Williams later in the same lecture: 

"We generally estimate the purity of the air by its fitness for the 
purposes of combustion, respiration, and animal life. And the more 
free it is from Phlogiston, the principle of inflammability, or any 
noxious effluvia or mixture, the more fit it is found for this purpose . . . 
Experiment. Take a receiver which holds one gallon and put a lighted 
candle into it, and let the air be confined. Effect: The candle will 
burn dimmer and dimmer until the light goe$ out. Observe the time, 
and this will be found to be in about one minute after it was put in. 
Remarks: It appears from this experiment that about one gallon of 
common air is requisite to support so small a fire or flame as that of 
this candle for the space of one minute. In this time the quantity of air 
is diminished by about 1/15 or 1/16 of its bulk." 

The diminution in bulk of the air, Professor Williams explains, is a 
consequence of the phlogistication of the air. For he says, "The greatest 
diminution of air by Phlogiston is about one-fourth of its first quantity 
and air which is diminished to its utmost by any one process cannot be 
any further diminished by another." 

Lavoisier's Broad Wording Hypothesis. The increase in weight of 
metals on calcination was, however, a quantitative observation that 
presented great difficulties to those who thought in terms of phlogiston. 
After the discovery of the compound nature of water, an explanation 
was contrived, but it had only a short life, for the phlogiston theory 
was then going to pieces rapidly, 

Lavoisier's new system of chemistry seems to have started with his 
pondering on the very large increase in weight when phosphorus was 
burned in air. In a sealed note deposited with the Secretary of the 
French Academy on November i, 1772, Lavoisier wrote: 

"About eight days ago I discovered that sulfur in burning, far from 
losing weight, on the contrary, gains it; it is the same with phosphorus; 
this increase of weight arises from a prodigious quantity of air that is 
fixed during combustion and combines with the vapors. 


"This discovery, which I have established by experiments, that I 
regard as decisive, has led me to think that what is observed in the 
combustion of sulfur and phosphorus may well take place in the case 
of all substances that gain in weight by combustion and calcination; 
and I am persuaded that the increase in weight of metallic calxes is 
due to the same cause." 

We seem to see here the flash of genius that puts forward a bold 
working hypothesis on a grand scale without much evidence to sup- 
port it. Yet there is no doubt, as Lavoisier always claimed, that the 
essential idea in his theory was contained in this note; something was 
taken up from the atmosphere in combustion and calcination. This was 
exactly opposite, be it noted, to the phlogiston doctrine. But what was 
the something? Lavoisier experimented with gases In a search for the 
answer without much success until the winter of 1774-1775. His book 
recounting his experiments (largely a repetition of the work of Joseph 
Black 2 and Priestley), published in 1774, gives the details of his ex- 
periment with phosphorus. (He never reported further on his experi- 
ments with sulfur, which were in part, at least, erroneous.) He con- 
vincingly demonstrates that the white solid produced when phosphorus 
burns in air confined over mercury weighs about twice as much as the 
phosphorus that produced it. But as to the nature of the "prodigious 
quantity of air" that is fixed in the process he remains uncertain. It 
was the experiments with red oxide of mercury that first put him on 
the right track. Perhaps it is not too much to say that the unique 
properties of this oxide made possible a relatively rapid advance in the 
chemistry of combustion. For no other oxide among all those known 
even today has the properties of (a) decomposing into the metal and 
oxygen when heated alone below "red heat"; (b) being readily pre- 
pared free from carbonate; (<r) being formed when the metal is heated 
in air at atmospheric pressure. 

For a successful investigation a chemist should have pure chemical 
compounds; mixtures of compounds are very baffling. Furthermore, 
he must study, if possible, relatively simple reactions that yield only a 
few products. If by changing the conditions the reaction can be re- 
versed (i.e., be made to run in the other direction) so much the better, 
for he can then proceed by synthesis and analysis. For example, in the 

2 Joseph Black (1728-1799), Professor of Anatomy and Chemistry at Glasgow, 
later Professor of Chemistry at Edinburgh. His work on latent and specific 
heats (see Case 3 of this series) was of first importance in the development 
of eighteenth-century physics. His investigation of the process of preparing 
lime from limestone was a model for later chemical investigations; from him 
Lavoisier learned the significance of the quantitative study of a simple chemical 
reaction (limestone -> lime + carbon dioxide) that could be reversed. 

74 CASE 2 

case of the red oxide of mercury, he can start with mercury and 
oxygen and prepare the oxide, or conversely, he can start with the red 
oxide and prepare mercury and oxygen. 


We now come to the crucial events in the chemical revolution 
(the overthrow of the phlogiston theory), namely, the effective dis- 
covery of oxygen. The following chronology of events may prove a 
useful guide. 

February 1774. The French chemist, Bayen, calls attention to the 
fact that red oxide of mercury yields mercury when heated alone (no 
charcoal needed as with other calxes) . He erroneously identifies the gas 
evolved as "fixed air" (carbon dioxide) ! 

August 1774. Priestley prepares oxygen by heating red oxide of 
mercury, but mistakes the new gas for "laughing gas." 

October 1774. Priestley tells Lavoisier of his experiment. 

March 1775. Priestley makes the effective discovery of oxygen. 

Easter 1775. Lavoisier communicates his memoir "On the Nature of 
the Principle which Combines with Metals during Calcination and 
Increases their Weight" to the French Academy. 

November 1775. Priestley corrects, in print, Lavoisier's faulty inter- 
pretation of the experiment. 

May 1777. Lavoisier communicates to the French Academy his 
memoir on respiration of animals; his ideas about oxygen are now clear. 

August 1778. Lavoisier publishes his revised "Easter Memoir." 

In order to read intelligently the papers by Lavoisier and Priestley 
dealing with the discovery of oxygen, a few facts about the oxides of 
nitrogen must be at hand. These facts are related to Priestley's "nitrous 
air test" for the purity of common air. Priestley had some years before 
prepared an oxide of nitrogen that plays an important part in this story; 
it is nitric oxide (NO), called by Priestley and his contemporaries 
"nitrous air." Priestley knew that this colorless gas, which is insoluble 
in water, when mixed with air produced a red gas ("red fumes") that 
was soluble in water. He found that air in which a candle had been 
burned until the flame went out would not produce soluble red fumes 
with "nitrous air." The reason for this, we now know, is that the re- 
action is between the "nitrous air" and the oxygen: 

2NO + O 2 - 

"nitrous air" plus oxygen yields "red fumes" that 

at once dissolve in water 

Since the product of this almost instantaneous reaction is soluble in 
water, it is evident that if the two gases are mixed over water there will 


be a diminution in volume. Indeed, if only the two pure gases were at 
hand and the volumes were chosen correctly, there would be no 
residual gas left after the reaction; the diminution would be complete. 
Since air is only about one-fifth oxygen, there will always be a large 
amount of residual gas when "nitrous air" and common air are mixed; 
the nitrogen does not react and is only very slightly soluble in water. 

Priestley conceived the idea of using this reaction to test the "good- 
ness" of common air. He found by repeated trials that with ordinary 
air (the best he knew) the maximum contraction occurred when one 
volume of "nitrous air" was mixed with two volumes of common air 
over water. Under these conditions the residue, measured a few 
minutes later, was only about 1.8 volumes. That is, the diminution in 
volume was as great as the whole volume of added "nitrous air" and 
about 20 percent more! With air that was thoroughly "bad" the final 
volume would be equal to the volume of the "nitrous air" plus the 
common air (three volumes). Intermediate values represented to 
Priestley intermediate grades of "goodness." This test was well known 
among chemical investigators since Priestley had published his results 
in 1772. It was therefore natural that not only Priestley himself but 
Lavoisier should apply the "nitrous air test" to any new "air" that 
would support combustion. 

Both Priestley and Lavoisier were at first misled by the application 
of this test to pure oxygen. Priestley corrected his own error, but 
Lavoisier interpreted the results correctly only after Priestley had 
publicly shown where the trouble lay. From the preceding paragraphs 
it will be evident to the reader that "nitrous air" and pure oxygen react, 
and when the reaction is carried out over water a large contraction in 
volume occurs. If Priestley's standard procedure for testing the good- 
ness of air is followed, one volume of "nitrous air" will be added to 
two volumes of oxygen. Under these conditions all the "nitrous air" is 
used up but a large amount of oxygen is left over. The actual diminu- 
tion in volume will be deceptively similar to that found when common 
air is at hand, but the residual gas instead of being nitrogen is oxygen. 
There is a small but significant quantitative difference. With common 
air the resulting gas the residue occupies only 1.8 volumes if 2.0 
volumes are initially employed; with pure oxygen the final volume is 
nearer 1.6 volumes. The fact that these numbers are as close as they 
are is more or less an accident since Priestley chose his standard oper- 
ating procedure purely empirically (by trial and error); with larger 
amounts o "nitrous air," the difference between common air and 
oxygen would be more apparent, as will be evident in a moment. At all 
events, both Priestley and Lavoisier overlooked the clue offered to them 

76 CASE 2 

by the somewhat larger diminution in volume of the new gas when 
subjected to Priestley's test for its "goodness." 

The striking contrast between the behavior of common air and 
oxygen when treated with "nitrous air" over water lies in the proper- 
ties of the residual gas. (This can be strikingly shown as a lecture-table 
demonstration, using graduated cylinders as containers in a pneumatic 
trough.) In the first case, nitrogen mixed with a little "nitrous air" is 
left; in the other, oxygen. Therefore, the residue in the one instance 
will support neither combustion nor animal life, nor will it react 
further with "nitrous air." In the other, the residue has all the properties 
of the original sample. Any one of the simple tests will at once make 
this striking difference apparent; a lighted candle, a live mouse, or the 
addition of "nitrous air" will convince anyone that the two samples of 
residual gas were totally different. But it never occurred to Lavoisier 
to try any of these experiments; nor did it occur to Priestley either. 
Only by the "accident" he describes (see Sec. 4) did Priestley come 
to examine what was left over when "nitrous air" had diminished his 
new air from red oxide of mercury! The fact that both investigators 
took the wrong turn in the road at a critical point in a study of the 
first importance illustrates how much more complicated is the advance 
of science than "collecting the facts, classifying the facts, formulating 
laws, and elaborating from the laws adequate theories." 

In comparing the work of Priestley and Lavoisier it is well to bear 
in mind the differences in their scientific experience up to the year 
1774. Priestley was then 41 years old and had started his study of 
"airs" (gases) some seven years before with an investigation of the 
fixed air generated in a brewery near his house in Leeds (where he was 
then the minister of a "dissenting" chapel). In the meantime, he had 
become the leading pneumatic chemist of the day, having improved 
the equipment for handling gases and discovered a number of new 
gases. Lavoisier, on the other hand, was not only ten years younger 
but a newcomer to the field of experimental chemistry who had only 
within the past two years repeated many of the early experiments on 
gases in order to learn the necessary techniques. Yet both the experi- 
enced older man and the brash young, inexperienced experimenter 
made essentially the same mistake and almost at the same moment. In 
both instances unconscious assumptions invalidated their chains of 

A few words are now in order about the two versions of Lavoisier's 
first communication of his experiments on oxygen. Lavoisier read his 
paper "On the Nature of the Principle which Combines with Metals 


during Calcination and Increases their Weight" for the first time to 
the French Academy of Science on Easter, 1775. (It is sometimes re- 
ferred to as the Easter Memoir of 1775.) It was immediately published, 
presumably in the form in which he read it, in the May 1775 number 
of the Journal de Physique (page 429). (This magazine was edited 
by Rozier and carried the full title Observations sur La Physique, sur 
UHistoire Naturelle et sur Les Arts et Metiers.} The official publi- 
cation of the Academy of Sciences, the Memoir es de V Academic des 
Sciences, was at that time months or years late in appearing; this fact 
gave the authors ample opportunity to revise their communications 
before their final and authoritative printing. Lavoisier's Easter Memoir 
of 1775 was again read to the Academy on August 8, 1778 and reedited 
at that time, incorporating a few very important changes. A comparison 
between the text in Rozier 's Journal of May 1775 and the official paper 
published after 1778 affords the rare opportunity previously mentioned 
of viewing a great discovery in the making. 

In the spring of 1775 Lavoisier just missed seeing the full significance 
of the experiments with the red precipitate of mercury (oxide of 
mercury) . He appears to have thought that he had common air at hand 
rather than a new gas; it was the experiment with Priestley's method 
of testing the "goodness" of an air by the use of "nitrous air" that was 
primarily responsible for his erroneous conclusion. For the sixth point 
in the first version of his paper (May 1775) states that the gas evolved 
from red oxide of mercury "was diminished like common air by an 
addition of a third of nitrous air." Priestley, on reading this sometime 
in the summer of 1775, hastened to record in a book of his, printed a 
few months later, that this was wrong (see Sec. 3). We cannot be 
certain that these words of his rival put Lavoisier back on the right 
track, but we find from Lavoisier's laboratory notebooks that in the 
following February (1776) he had prepared an "air" from a sample of 
red oxide of mercury and found it to be considerably "better" than 
common air by the test with "nitrous air" In May 1777, Lavoisier read 
to the Academy a paper on the respiration of animals in which he 
makes clear that air is a mixture of two gases, one "highly respirable," 
the other unable to support combustion or respiration. By 1778 there 
was no doubt in anyone's mind that a new gas, not common air, was 
produced on heating red oxide of mercury. Therefore, point 6 is com- 
pletely altered in the final version of the Easter Memoir, and of course 
so is the final conclusion. 

It is interesting to note how relatively few corrections and changes 
were required to make the original version of Lavoisier's paper cor- 
respond with the final and complete interpretation of his results. The 
similarity of the two versions is evidence that Lavoisier was very close 

78 CASE 2 

to his final goal. Yet the first version is almost self-contradictory, for 
the gas from the red oxide is "common air" yet also "purer than com- 
mon air." For the moment Lavoisier wanted to have it both ways! 
Though Lavoisier at first went wrong on an important point and was 
set right by Priestley, it was only Lavoisier., we must remember, who 
saw the real significance of the discovery of oxygen. He built the new 
facts into his own conceptual scheme and gave an enduring explana- 
tion of combustion. To Priestley goes the honor of being the effective 
discoverer of oxygen, but to the end of his life it was still "dephlogis- 
ticated air" to him. 

In the following translation the new words and sentences added to 
the May 1775 version (Rozier's Journal) by Lavoisier are enclosed in 
braces and printed in italics. The material deleted from this first version 
in the preparation of the second and final form of the communication 
is printed in boldface type. If the changes are extensive the two versions 
are printed in parallel columns, the first version being on the left. The 
footnotes and the explanatory material enclosed in brackets were 
written by the translator, the editor of this Case, to assist the reader. 


This memoir was read before the French Academy of Sciences 
at its Easter meeting in 1775, and again on August 8, 1778 (Memoir es de 
I' Academic des Sciences, 1775, p. 520). It carried the following footnote: 
"The first experiments relative to this Memoir were made more than a 
year ago; those on 'precipitate of mercury per se' were first attempted 
with a burning glass in the month of November, 1774, and continued 
with all precautions and necessary care in the laboratory of Montigny, 
conjointly with M. Trudaine on February 28 and March i and 2 of this 
year; finally they were once more repeated on the 3ist of last March in 
the presence of M. The Duke de la Rochefoucault, and MM. Trudaine, 
de Montigny, Macquer and Cadet." 

Memoir On The Nature Of The Principle Which Combines With 
Metals During Calcination and Increases Their Weight 

Are there different kinds of air? Does it suffice that a body should be 
in a state of permanent elasticity in order to be considered a kind of air? 
Are the different airs that nature offers us, or that we succeed in making, 
exceptional substances or modifications of atmospheric air? Such are the 
principal questions embraced in the plan I have formed and the problems 
which I propose to develop [in succession] before the Academy. But 
since the time devoted to our public meetings does not allow me to treat 
any one of these questions in full, I will confine myself today to one 
particular case, and will limit myself to showing that the principle which 


unites with metals during calcination, which increases their weight, and 
which is a constituent of the calx is 

neither one of the constituent parts {nothing else than the healthiest 
of the air, nor a particular acid and purest part of air; so that ij 
distributed in the atmosphere, that air, after entering into combination 
it Is the air itself entire without with a metal, is set free again, it 
alteration without decomposition emerges in an eminently respirable 
even to the point that if one sets It condition, more suited than at- 
free after it has been so combined mospheric air to support ignition 
it comes out more pure, more re- and combustion^] 
spirable, if this expression may be 
permitted, than the air of the at- 
mosphere and is more suitable to 
support ignition and combustion. 

The majority of metallic calces are only reduced, that is to say, only 
return to the metallic condition, by immediate contact with a carbona- 
ceous material, or with some substance containing what is called phlogis- 
ton. The charcoal that one uses is entirely destroyed during the operation 
when the amount is in suitable proportion, whence it follows that the 
air set free from metallic reductions with charcoal is not simple; it is in 
some way the result of the combination of the elastic fluid set free from 
the metal and that set free from the charcoal; thus, though this fluid is 
obtained in the state of fixed air, one is not justified in concluding that it 
existed in this state in the metallic calx before its combination with the 

These reflections have made me feel how essential it is, in order to 
unravel the mystery of the reduction of metallic calces, that all my 
experiments be performed on cakes which can be reduced without any 
addition [that is, without the addition of charcoal]. The calces of iron 
have this property: in fact, all those, whether natural or artificial, which 
we have placed in the focus of a burning glass either that of M. the 
Regent or of M. de Trudaine, in each case were totally reduced without 

In consequence, I tried with the aid of a burning glass to reduce 
several kinds of iron calces under large glass bell-jars turned upside 
down in mercury, and by this method I succeeded in setting free a large 
quantity of elastic fluid {air}; but, as at the same time this elastic fluid 
{air} mixed with the common air contained in the bell, this circum- 
stance cast great uncertainty on my results; none of the experiments to 
which I submitted this air was completely conclusive, and it was im- 
possible to be sure whether the phenomena obtained depended on the 
common air, on that released from the iron calces, or on the combination 
of the two together. These experiments not having fulfilled my object, I 
omit the details here; they will find their natural place in other memoirs. 
[Those who have studied Case i of this series will be interested in com- 
paring this method of reporting with that used by Boyle concerning his 
experiments with the subtle fluid.] 

80 CASE 2 

Since these difficulties proceeded from the very nature of iron, from 
the refractory quality of its calces, and from the difficulty of reducing 
them without addition, I considered them as insurmountable, and 
henceforth decided to address myself to another kind of calx more easily 
treated and which, like iron calces, possessed the property of being re- 
duced without addition, Mercurius caldnatus per se, which is nothing 
else than a calx of mercury, as several authors have already maintained 
and as the reader of this Memoir will be even convinced, mercurius 
caldnatus per se, I repeat, seemed to me completely suitable for what I 
had in view; no one today is unaware that this substance can be reduced 
without addition at a very moderate degree of heat. Although I have 
repeated many times the experiments I am going to report, I have not 
thought it necessary to give particular details of any of them here, for 
fear of occupying too much space, and I have therefore combined into 
one account the observations made during several repetitions of the same 

Throughout this memoir Lavoisier is referring to only one com- 
pound of mercury, namely the red oxide; he refers to it as precipitated 
mercury per se, to indicate that it was obtained by heating mercury by 
itself. We have translated it as mercurius caldnatus per se f the Latin 
phrase used by Priestley to describe the same material. 

In order to be sure that mercurius caldnatus per se was a true metallic 
calx, whether it would give the same results and the same kind of air 
on reduction, I tried at first to reduce it by the ordinary me.thod, that 
is to say, to use the accepted expression, by the addition of phlogiston. 
I mixed one ounce of this calx with 48 grains 3 of powdered charcoal, 
and introduced the whole into a little glass retort of at most two cubic 
inches capacity, which I placed in a reverberatory furnace of propor- 
tionate size. The neck of this retort was about a foot long, and three to 
four lines in diameter [a line is one- twelfth of an inch] ; it had been 
bent in different places by means of an enameler's lamp, and its tip was 
such that it could be fixed under a bell-jar of sufficient size, filled with 
water, (and turned upside down in a trough of water. The apparatus 
now before the eyes of the Academy suffices to give an idea of the 
operation.} This apparatus, simple as it is, is the more exact that there is 
no soldering or luting or any passage through which air might leak in 
or escape. 

As soon as a flame was applied to the retort and the heat had begun 
to take effect, the ordinary air contained in the retort expanded, and a 
small quantity passed into the bell-jar; but in view of the small size of 
the part of the retort that remained empty, this air could not introduce 

8 The system of weights employed was: i pound (Paris standard) = 16 ounces; 
i ounce = 8 gros; i gros = 72 grains; or i pound (Paris) =9216 grains. The 
English avoirdupois pound of 16 ounces (still commonly used) is somewhat 
lighter, and is divided into 7000 grains. 


a sensible error, and at the most it could scarcely amount to a cubic inch. 
When the retort began to get hotter, air was very rapidly disengaged 
and rose through the water into the bell-jar; the operation did not last 
more than three-quarters of an hour, the flame being used sparingly 
during this interval. When all the calx of mercury had been reduced and 
the air ceased rising, I marked the height at which the water stood in the 
bell-jar and found that the quantity of air set free amounted to 64 cubic 
inches, without allowing for the volume necessarily absorbed in passing 
through the water. 

I submitted this air to a large number of tests, which I will not describe 
in detail, and found (i) that it was susceptible to combination with 
water on shaking and gave to it all the properties of acidulated, gaseous, 
or aerated waters such as those of Seltz, Pougues, Bussang, Pyrmont, etc.; 
(2) that animals placed in it died in a few seconds; (3) that candles 
and all burning bodies were instantly extinguished in it; (4) that it pre- 
cipitated lime water; (5) that it combined very easily with either the 
fixed or the volatile alkalis, removing their causticity and giving them 
the property of crystallizing. [Fixed alkalis are materials like slaked lime 
or caustic soda that absorb carbon dioxide to form carbonates which, 
unlike the alkalis, are not caustic amorphous solids but noncaustic crystal- 
line solids; volatile alkali is ammonia.] All these are precisely the 
qualities of the kind of air known as fixed air, 

or mephltic air such as is obtained [obtained by the reduction of 
from all metallic calces by the ad- minium [an oxide of lead] by 
dition of charcoal such as is set powdered charcoal,} such as is set 
free from fermenting matters. It free {from calcareous earths and 
was thus unquestionable that mer- effervescent alkalis by their com- 
curius calcinatus per se should be blnatlon with acids, or} from 
included in the category of metal- fermenting {vegetable} matters, 
lie calces. {etc.}. It was thus unquestionable 

that mercurius calcinatus fer se 
{gave the same products as other 
metallic calces on reduction with 
addition of phlogiston and that it} 
should {consequently} be included 
in the {general} category of metal- 
lic calces. 

Lavoisier up to this point has added nothing new. Bay en, another 
French chemist, had recently reported similar results; Lavoisier's work 
represented a careful rechecking. How important such independent 
verification may be is evident from what follows. For Bayen had re- 
ported that the gas evolved when the mercury calx was heated by itself 
was also fixed air! How he could come to such an erroneous conclu- 
sion no one knows, but he was obviously not a skillful experimenter 
with gases. 

82 CASE 2 

It remained only to examine this calx alone, to reduce it without 
addition, to see if some air [elastic fluid} would be set free, and if so, to 
determine what state It was In {its nature}. To accomplish this I put 
into a retort of the same size as before (two cubic inches) one ounce of 
mercurius caldnatus per se, alone; I arranged the apparatus in the same 
way as for the preceding experiment, so that all the circumstances were 
exactly the same; the reduction was a little more difficult than with the 
addition of charcoal; it required more heat and there was no perceptible 
effect till the retort began to get slightly red-hot; then air was set free 
little by little, and passed into the bell-jar, and the same degree of heat 
being maintained for 2 1 A hours, all the mercurius caldnatus per se was 

The operation completed, 7 gros, 18 grains of {liquid} mercury were 
found, partly in the neck of the retort and partly in a glass vessel which 
I had placed at the tip of the retort under the water; the amount of air 
in the bell-jar was found to be 78 cubic inches; from which it follows, that 
supposing all the loss of weight is attributed to the air, each cubic inch 
must weigh a little less than two-thirds of a grain, which does not differ 
much from the weight of ordinary air. 

Having established these first results, I hastened to submit the 78 cubic 
inches of air I had obtained to all the tests suitable for determining its 
nature, and I found, much to my surprise: 

d) that it was not susceptible to (i) that it was not susceptible to 
combination with water upon combination with water upon 
shaking; shaking; 

(2) that it did not precipitate (2) that it did not precipitate 
lime water; lime water {but only made it tur- 
bid to an almost imperceptible 

(3) that it did not combine with (3) that it did not combine with 
fixed or volatile alkalis; fixed or volatile alkalis; 

(4) that it did not at all diminish (4) that it did not at all diminish 
their caustic qualities; their caustic qualities; 

[these first four tests were designed to show whether the gas was in 
whole or part "fixed air" as Bayen had reported; obviously it was not;] 

(5) that it could be used again (5) that it could be used again 
for the calcination of metals; for the calcination of metals; 

(6) that it was diminished like 
common air by an addition of a 
third of nitrous air; 4 

* "Addition of a third of nitrous air" means that one volume of "nitrous air" 
to two volumes of air to be tested was used the mixture being, of course, 
allowed to stand over water. 


finally, that it had none of the (6) finally, that it had none of 
properties of fixed air: far from the properties of fixed air: far 
causing animals to perish, it from causing animals to perish, 
seemed on the contrary more it seemed on the contrary more 
suited to support their respiration; suited to support their respiration; 
not only were candles and burning not only were candles and burn- 
objects not extinguished in it, but ing objects not extinguished in it, 
the flame increased in a very re- but the flame increased in a very 
markable manner and gave much remarkable manner and gave 
more light than in common air. much more light than in common 

air; {charcoal burned in it with a 
radiance almost li%e that of phos- 
phorus, and all combustible bodies 
in general were consumed with 
astonishing speed.} All these cir- 

All these circumstances convinced cumstances convinced me fully 
me fully that this air was not only that this air, {far from being fixed 
common air but that it was more air, was in a state more respirable 
respirable, more combustible, and and more combustible,} and con- 
consequently that it was more pure sequently that it was more pure 
than even the air in which we live, than even the air in which we live. 

It seems proved accordingly that the principle which combines with 
metals during calcination and which augments their weight is nothing 
else than the purest part of the very air which surrounds us, which we 
breathe, and which in this operation passes from a condition of elasticity 
to that of solidity; if then it is obtained in the form of fixed air in all 
the metallic reductions in which charcoal is used, this effect is due to 
the charcoal itself {the combination of the latter with the pure part of the 
air}, and it is very likely that all metallic calces, like that of mercury, 
would give only common air {only eminently respirable air} if they 
could all be reduced without addition like mercurius calcinatus per $e. 

The nitre referred to in the next paragraph is potassium nitrate, a 
compound of the metal potassium, oxygen, and nitrogen; from it 
chemists early learned to prepare nitric acid and hence other nitrates. 
Mixed with charcoal and sulfur it yields black gunpowder. This para- 
graph, which deals with the explosion of powder, may be omitted. 

Everything that has been said of the air from metallic calces may 
naturally be applied to that obtained from nitre by detonation; we know 
from a number of experiments already published, the majority of which 
I have repeated, that most of this air is in the form of fixed air, that it is 
fatal to any animal breathing it, that it has the property of precipitating 
lime water and of combining with lime and alkalis, of softening them 
and making them crystallize; but since the detonation of nitre only 
takes place after the addition of charcoal or of some body which contains 

84 2 

phlogiston. It Is very probable {it cannot be doubted] that in this cir- 
cumstance also common air {eminently respirable air] is converted into 
fixed air; 

from which it follows that the air 
combined with nitre which pro- 
duces the terrible explosions of 
gunpowder is common atmos- 
pheric air deprived of its elasticity. 
From the fact that common air 
changes to fixed air when com- 
bined with charcoal It would seem 
natural to conclude that fixed air 
Is nothing but a combination of 
common air and phlogiston. This 
Is Mr. Priestley's opinion and It 
must be admitted that it Is not 
without probability; however, 
when one looks into the facts in 
detail, contradictions arise so fre- 
quently I feel It necessary to ask 
natural philosophers and chemists 
still to suspend judgment; I hope 
to be soon In a position to com- 
municate the reasons for my 

from which it follows that the air 
combined with nitre which pro- 
duces the terrible explosions of 
gunpowder is {the res fir able part 
of} atmospheric air deprived of its 
elasticity {and which is one of the 
constituent principles of nitric 
acid. Since charcoal disappears 
completely in the revivification of 
mercuric calx and since only mer- 
cury and fixed air are produced by 
this operation, one is forced to 
conclude that the principle to 
which has hitherto been given the 
name of fixed air, is the result of 
the combination of the eminently 
respirable portion of the air with 
charcoal; and this is what I pro- 
pose to develop in a more satisfac- 
tory manner in subsequent me- 
moirs which 1 shall devote to this 
object. } 

A diagram of the apparatus used by Lavoisier in reducing red oxide 
of mercury with and without the addition of charcoal is shown in 
Fig. i. The use of a reverberatory furnace (that is, one in which the 
heat is reflected down on the retort as well as coming from the flame 
below) enabled Lavoisier to heat the retort to a dull red heat. This 
temperature is required for the decomposition of the oxide if no char- 
coal is employed. Lavoisier does not state in this paper how he removed 
samples of the gas for the various tests, but in some of his later equip- 
ment the gas was removed through a small orifice near the top of the 
bell jar to smaller vessels by a suitable suction device. The methods of 
collecting gases over water or mercury and transferring them from one 
vessel to another had been greatly improved by Joseph Priestley a 
short time before. 

The paragraph on page 82 in which Lavoisier records the weight of 
mercury recovered from the decomposition of the oxide and the amount 
of gas evolved is of great significance. Here Lavoisier is invoking a 
principle that underlay his whole work. One biographer of the French 
chemist, recalling that Lavoisier was a man of business affairs first 
and a chemist second, has spoken of Lavoisier's "principle of the 



balance sheet." Lavoisier had early in his career used the balance, and 
in repeating Joseph Black's work had undoubtedly been impressed by 
the Scotch chemist's success in accounting for the weights of the 
starting materials and of the products in a chemical reaction. In the 

FIG. i. Diagram of apparatus used by Lavoisier in collecting di gas evolved 
when red oxide of mercury is heated. 

paragraph mentioned we see Lavoisier in his first major chemical 
contribution comparing the weight of the initial oxide (i ounce) with 
the mercury produced (7 gros 18 grains) and deducing that the only 
other product (the gas) must account for the difference in weight 
(i ounce = 8 gros and i gros = 72 grains; therefore the difference 
would be 7 gros 72 grains minus 7 gros 18 grains = 54 grains). He 
concludes that the 78 cubic inches of the air evolved must weigh 54 
grains or about 54/78 grain per cubic inch (54/78 is a little more than 
2/3, which is 52/78). 

The weight of i cubic inch of air at the usual temperature and 
pressure of a laboratory had been given as 0.46 (or 36/78) grain by 
Lavoisier in a book published a few years earlier. Therefore, his state- 
ment that the estimated weight of 2/3 grain per cubic inch "does not 
differ much from the weight of ordinary air" is an optimistic state- 
ment by an investigator looking for an agreement between two num- 
bers. Lavoisier was aware, of course, that this estimate of the density 

86 CASE 2 

of the air was extremely rough, for his method of insuring the collec- 
tion of all the mercury was far from sufficient for the purposes. (Note 
that the weight of the air evolved was a small difference between two 
relatively large numbers; such a situation is always unfavorable for 
accurate measurements. The failure to collect 3 percent, or 16 grains, 
of the mercury would have increased the estimated weight of the total 
gas by that amount, or by 16/78 grain per cubic inch, which is about 
the discrepancy observed.) Lavoisier does not record the pressure or 
temperature, though he does so in all his later experiments, where his 
calculations can be made with a higher degree of accuracy. The sig- 
nificance of the paragraph lies, therefore, not in the result, which is 
far too approximate to be useful, but in Lavoisier's mode of reasoning. 
Within the limits of experimental error he is trying to apply the 
principle of the balance sheet. 

In his textbook of 1789 Lavoisier wrote: "We must lay it down as 
an incontestable axiom, that in all the operations of art and nature, 
nothing is created; an equal quantity of matter exists both before and 
after the experiment . . . Upon this principle, the whole art of per- 
forming chemical experiments depends." Whether or not Lavoisier 
came to this principle because as a member of the firm that collected 
taxes he was used to balancing his books in terms of money, the 
principle was the foundation of his work. In the nineteenth century 
the exactness of this principle was tested by very careful experimenta- 
tion, using balances far more sensitive than those available in Lavoisier's 
time. In every case it was found that the weight of the factors was 
equal to that of the products within the small experimental error of 
the measurements. The principle was thus considered a generalization 
of experimental fact, rather than an axiom; it became known as the 
Law of Conservation of Mass (or Matter) . We now have good reason 
to believe on both theoretical and experimental grounds that in the 
form in which it was expressed by Lavoisier and by the scientists of 
the nineteenth century it is only an approximation. Whenever energy 
is released or absorbed in a chemical change (and that is in practically 
every instance) a very very small change in mass occurs; the change 
is too small to be detected even with the most accurate measurements 
of the weights involved in even the most energetic chemical reaction. 
Those changes, however, that take place when the nuclei of atoms are 
altered liberate amounts of energy of another order of magnitude from 
those connected with chemical reactions; in this case the change of 
mass is significant and is directly related to the energy evolved. It is 
common nowadays to speak of the combination in the twentieth cen- 
tury of the two principles of conservation of mass and of conservation 
of energy into one the principle of conservation of mass and energy. 


This doctrine is accepted as a guiding principle by physicists and 
chemists today. 

Those who have some knowledge of quantitative chemistry will 
interpret the equations given on page 69 for the reduction of mercury 
oxide with and without charcoal as stating that the volumes of oxygen 
and of carbon dioxide produced from i ounce of oxide should be the 
same (at the same temperature and pressure). Actually Lavoisier ob- 
tained 64 cubic inches of carbon dioxide and 78 of oxygen; the differ- 
ence is due to the solubility of carbon dioxide in water. Indeed, if the 
gas had been allowed to stand over the water for any length of time 
or had been shaken with it, almost all of it would have gone into 
solution. In later experiments Lavoisier collected carbon dioxide over 
mercury. In this memoir we see him struggling with the difficulties of 
carrying out chemical experiments in such a way as to make quanti- 
tative observations meaningful. This is the beginning of the long and 
arduous road that had to be traveled before chemistry could become a 
quantitative science. 

Lavoisier's reasoning in 1775 and 1778 is worth examining with 
some care. His broad working hypothesis of 1772 was that "something" 
was taken up from the air when a metal was calcined. At first he 
thought that this "something" might be fixed air and had experimented 
in vain to prove this. In other words, his broad working hypothesis, 
when made specific by substituting the words "fixed air" for "some- 
thing," yielded deductions that were not confirmed by experimental 
test. Now, thanks perhaps to the unconscious tip that Priestley had 
conveyed to him in conversation in the fall of 1774, he had a calx which 
on heating yielded a gas that behaved like common air. Substituting 
common air for the "something" in his broad working hypothesis 
yielded a deduction that appeared to be confirmed by the experiment. 
But note carefully that deductions from broad working hypotheses are 
never directly confirmed or negated. A specific experiment must 
always be related to the deductions by one or more limited working 
hypotheses. This is where the difficulties arise and in this case we can 
see exactly how they arose in 1775. Of the six tests recorded by Lavoisier 
in his first version of the Easter Memoir, the first four gave convincing 
evidence that the gas was not fixed air. (In each test a limited working 
hypothesis was implicit, an "if . . . then" type of reasoning was em- 
ployed.) The fifth and sixth tests, together with the experiments with 
the candle and with animals, seemed to provide conclusive evidence 
that the gas was common air. On the supposition that the gas was 
common air, Lavoisier could say, "If I perform the following manipu- 
lations, then the result will be such and such." (This last is a limited 
working hypothesis that is confirmed or negated by test.) In other 

88 CASE 2 

words, there is the haunting question whether another substance could 
also behave in this same manner; of these tests the nitrous air test ap- 
peared to be the most specific and must have appealed to Lavoisier 
because it was at least roughly quantitative. But the similarity in be- 
havior o the new gas and common air in this test was, we have seen, 
only apparent. The assumption that there would be no further diminu- 
tion in volume if more nitrous air were added was implicit in the 
report of Easter 1774, for that was the case with common air. Priestley, 
as we shall see in the next section, corrected the assumption as a result 
of an accident; Lavoisier corrected it after having learned of Priestley's 
use of the nitrous air test to show that the gas was not common air. 

As far as the significance of the nitrous air test was concerned, both 
Priestley and Lavoisier agreed by the spring of 1776. They would now 
say that an air is common air if it is diminished by a third of nitrous 
air, provided it is not further diminished on adding more nitrous air. 
They would both agree that a new air was present when the calx of 
mercury was heated. But as to the broad working hypothesis of La- 
voisier, they disagreed completely. Priestley stuck to the conceptual 
scheme in which phlogiston was the determining factor in calx forma- 
tion. Lavoisier saw his broad working hypothesis now made specific by 
substituting the words "a constituent of the atmosphere which supports 
combustion" for his "something." His working hypothesis on a grand 
scale was about to attain the status of a new conceptual scheme. 


Priestley's comments on Lavoisier's paper were printed in 
Section XVI of Volume II of his Experiments and Observations on 
Different Kinds of Air the dedication of which is dated November i, 
1775. The title of this section, one of the last in the book, is "An Ac- 
count of some Misrepresentations of the Author's Sentiments, and of 
some Differences of Opinion with respect to the Subject of Air." The 
relevant passages (from pages 320-323) follow 5 (the words included in 
brackets have been added to enable the reader to follow the discussion 
in modern terms) ; the opening words refer to a discussion of Lavoisier's 
remark about Priestley's opinion as to the relation of fixed air to 
phlogiston, which is not relevant to the discussion of the experiments. 

Having mentioned the paper of Mr. Lavoisier's, published in Mr. 
Hosier's Journal, I would observe, that it appears by it, that, after I left 
Paris, where I procured the mercurius calcinatus [red oxide of mercury] 
above mentioned, and had spoken of the experiments that I had made, 
and that I intended to make with it, he began his experiments upon the 

8 All extracts from Priestley's book used in this Case are taken from the second 
edition (1776). 


same substance, and presently found what I have called dephlogisticated 
air [oxygen], but without investigating the nature of it, and indeed, 
without being fully apprised of the degree of its purity. For he had only 
tried it with one-third of nitrous air, and observed that a candle burned 
in it with more vigour than in common air; and though he says it seems 
to be more fit for respiration than common air, he does not say that he 
had made any trial how long an animal could live in it. 

Priestley felt he had been unfairly treated by Lavoisier because the 
French chemist made no mention in his paper of the facts communi- 
cated to him in the fall of 1774 by Priestley. Historians have been dis- 
cussing ever since how essential this verbal communication was in fact. 
The incident, quite apart from the entertaining way in which Priestley 
rebukes Lavoisier, is of interest as illustrating the state of scientific 
communication toward the end of the eighteenth century. As in the 
seventeenth century, investigators did not feel under any special obli- 
gation to refer to the work of others. Lavoisier makes no mention of 
Bayen's paper published a year before; possibly he assumed that every- 
body had read it. Since the middle of the nineteenth century, practice 
has changed in this respect. Investigators are today very scrupulous in 
referring to published work and even verbal communications. 

He therefore inferred, as I have said that I myself had once done, 
that this substance had, during the process of calcination, imbibed 
atmospherical air, not in part, but in whole. But then he extends his 
conclusion, and, as it appears to me, without any evidence, to all the 
metallic calces; saying that, very probably, they would all of them yield 
only common air, if, like mercurius calcinatus, they could be reduced 
without addition. For he considers the fixed air [carbon dioxide], which 
is yielded by most of them, to come from the charcoal, made use of to 
revivify the calx. Whereas it will be seen, in the course of my experi- 
ments, that several of those calces yield fixed air by heat only, without 
any addition of charcoal [that is, without addition of charcoal before 
being heated. Priestley was in error here; Lavoisier was right. Those 
calces from which Priestley obtained fixed air (carbon dioxide) were 
impure; they contained carbonates which are decomposed on heating 
yielding carbon dioxide]. 

He adds, that since common air is changed into fixed air when it is 
combined with charcoal, it would seem natural to conclude, that fixed 
air is only a combination of common air and phlogiston (an opinion 
which, as has been seen before, he ascribes to me) and it is not, he says, 
without probability; but adds, that it is so often contradicted by facts, 
that he desires philosophers and chymists to suspend their judgments; 
hoping that it will soon be in his power to explain the motives of his 
doubts. I, for one, am waiting with some impatience for this explanation. 
[But when it came, Priestley rejected it!] 

Mr. Lavoisier also concludes, from his observations, that the air pro- 

90 CASE 2 

duced by the detonation of nitre and the firing of gunpowder is common 
air. When he sees this volume of mine, he will, I doubt not, be convinced 
of the imperfection of his theory, and of this mistake, which he has been 
led into by means of it. [The detonation of nitre is not relevant to the 
case at hand.] 

Mr. Lavoisier as well as Sig. Landriani, Sig. F. Fontana, and indeed 
all other writers except myself, seems to consider common air (divested 
of the effluvia that float in it, and various substances that are dissolved 
in it, but which are in reality foreign to it) as a simple elementary body; 
whereas I have, for a long time, considered it as a compound; and this 
notion has been of great service to me in my inquiries. 

As a concurrence of unforeseen and undesigned circumstances has 
favoured me in this inquiry, a like happy concurrence may favour Mr. 
Lavoisier in another; and as, in this case, truth has been the means of 
leading him into error, error may, in its turn, lead him into truth. It will 
have been seen, in the course of my writings, that both these circum- 
stances have frequently happened to myself; and indeed examples of 
both of them will be found in my first section concerning this very 
subject of dephlogisticated air. 

It is pleasant when we can be equally amused with our own mistakes, 
and those of others. I have voluntarily given others many opportunities 
of amusing themselves with mine, when it was entirely in my power to 
have concealed them. But I was determined to shew how little mystery 
there really is in the business of experimental philosophy, and with how 
little sagacity, or even design, discoveries (which some persons are 
pleased to consider as great and wonderful things) have been made. 


Having read Priestley's comments written in the summer of 
1775 on Lavoisier's Easter Memoir of the same year, we are ready to 
examine the record of how Priestley himself at first erroneously in- 
terpreted his experiments with oxygen. In the summer of 1774 he first 
started studying the gas evolved when red oxide of mercury is heated, 
as he relates in the account reproduced here. 

A few words of explanation are required to make clear to the reader 
who has little or no knowledge of chemistry how Priestley made his 
first error, which was a completely erroneous identification of the new 
gas. He tested the "new air" (which was in reality oxygen) with a 
lighted candle and found that the candle was not extinguished but 
burned brightly. Now a few years before, Priestley had prepared an 
oxide of nitrogen that has the unusual property of supporting com- 
bustion. He did not know, of course, that it was an oxide of nitrogen, 
but he called it "phlogisticated nitrous air" for he had prepared it by 
letting "nitrous air" (nitric oxide) stand with metallic iron or certain 



other substances which decompose the nitric oxide, taking away some 
of the oxygen and yielding the other oxide, which supports combustion. 
Although in Priestley's terminology it was "phlogisticated," he appar- 
ently gave no explanation of why phlogistication made the nitrous air 
inflammable. The chemical reaction is as follows: 


2ND + Fe - N 2 O + FeO 

"nitrous air," plus metallic yields "phlogisticated plus iron 

colorless, in- iron nitrous air" oxide 

soluble gas ; will ( modern name : 

not support nitrous oxide) 

combustion somewhat soluble 

in water; sup- 
ports combustion; 
commonly called 
"laughing gas" 

The product we now call nitrous oxide; this modern name is confusing 
in this narrative, since in Priestley's day our modern nitric oxide was 
called "nitrous air." Fortunately, nitrous oxide plays only a minor role 
and will hereafter be designated as "laughing gas," for it is often so 
called from the fact that today it is used for anesthesia, particularly 
by dentists, and the patient sometimes becomes quite merry before the 
anesthesia is complete! Priestley's sample of this gas was a mixture of 
the original nitric oxide and "laughing gas." When the mixture was 
agitated with water, the oxide that supports combustion was dissolved. 
The significance of this fact will be evident in what follows. 

Priestley's account of his experiments leading to the identification of 
oxygen as a new gas are described in Section III of Volume II of his 
Experiments. After some rather amusing general remarks about ex- 
perimental difficulties, he recounts the experiments performed in 1774 
and the totally erroneous conclusions he drew from them. (It was at 
this time that he confused oxygen with "phlogisticated nitrous air," 
that is, "nitrous air exposed to iron.") On March i, 1775 Priestley de- 
cided to apply his "nitrous air test" to the "air" obtained from the red 
oxide. The results of this experiment showed that the new "air" was 
at least very much like common air. It is a remarkable coincidence that 
Lavoisier almost simultaneously and quite independently was per- 
forming the same experiment; he decided on the basis of the result that 
he had at hand a purified common air, as is evident from the first 
version of his memoir. But Priestley, more or less by accident, went 
further. He found that the residual gas, or air, left after the reaction 
with nitrous air and the subsequent diminution in volume would still 

92 CASE 2 

allow a candle to burn brightly. This accidental discovery was fol- 
lowed up by experiments with a mouse which, he found, would live in 
this residual gas. Priestley then began to suspect that the air under in- 
vestigation not only was at least as good as common air but might be 
better. This he proved by showing that even after a mouse had lived 
in it for some time, the nitrous air diminished its volume more than 
common air. 

"Being now fully satisfied of the superior goodness of this kind of 
air," he found by careful trials with increasing amounts of nitrous air 
that he could get an increasing diminution in volume until more than 
four half measures (for one measure of the gas being tested) were used. 
This proved that a substance quite different from common air was at 
hand. The effective discovery of oxygen by Priestley had occurred. 

Priestley's own account now follows (pages 29-49 f Volume II). 
The material in brackets is added to assist the reader. 

General Observations on the Role of Chance Discoveries 

The contents of this section will furnish a very striking illustration of 
the truth of a remark, which I have more than once made in my 
philosophical writings, and which can hardly be too often repeated, as it 
tends greatly to encourage philosophical investigations; viz. that more is 
owing to what we call chance, that is, philosophically speaking, to the 
observation of events arising from unknown causes, than to any proper 
design, or pre-conceived theory in this business. This does not appear in 
the works of those who write synthetically upon these subjects; but 
would, I doubt not, appear very strikingly in those who are the most 
celebrated for their philosophical acumen, did they write analytically 
and ingenuously. 

For my own part, I will frankly acknowledge, that, at the commence- 
ment of the experiments recited in this section, I was so far from having 
formed any hypothesis that led to the discoveries I made in pursuing 
them, that they would have appeared very improbable to me had I been 
told of them; and when the decisive facts did at length obtrude them- 
selves upon my notice, it was very slowly, and with great hesitation, that 
I yielded to the evidence of my senses. And yet, when I re-consider the 
matter, and compare my last discoveries relating to the constitution of 
the atmosphere with the first, I see the closest and the easiest connexion 
in the world between them, so as to wonder that I should not have been 
led immediately from the one to the other. That this was not the case, 
I attribute to the force of prejudice, which, unknown to ourselves, biasses 
not only our judgments, properly so called, but even the perceptions of 
our senses: for we may take a maxim so strongly for granted, that the 
plainest evidence of sense will not intirely change, and often hardly 
modify our persuasions; and the more ingenious a man is, the more 


effectually he is entangled in his errors; his ingenuity only helping him 
to deceive himself, by evading the force of truth. 

These observations of Priestley's have been the basis for some 
criticism of his scientific judgment by historians of science. As in some 
of the comments on the accidental nature of his experiments later in 
this same account, Priestley is here frank almost to the point of naivete. 
Yet anyone conversant with the way chemical discoveries are made 
even today will hardly take exception to his remarks. 

Priestley's Views on the Nature of the Atmosphere 

In the following passage, Priestley refers to "agitation in water" as a 
method of purifying a gas. In this process, for which he had invented 
an apparatus, two things happened of which he was ignorant and both 
of which made the gas more fit for respiration. One was the dissolving 
in the water of the carbon dioxide in the gas; the other was the 
addition to the gas of some oxygen, which came from the dissolved 
air present in ordinary samples of water. Priestley is quite correct in 
what he says about the "process of vegetation"; green plants not only 
use up carbon dioxide but evolve oxygen. 

There are, I believe, very few maxims in philosophy that have laid 
firmer hold upon the mind, than that air, meaning atmospherical air 
(free from various foreign matters, which were always supposed to be 
dissolved, and intermixed with it) is a simple elementary substance, 
indestructible, and unalterable, at least as much so as water is supposed 
to be. In the course of my inquiries, I was, however, soon satisfied that 
atmospherical air is not an unalterable thing; for that the phlogiston with 
which it becomes loaded from bodies burning in it, and animals breathing 
it, and various other chemical processes, so far alters and depraves it, as 
to render it altogether unfit for inflammation, respiration, and other 
purposes to which it is subservient; and I had discovered that agitation 
in water, the process of vegetation, and probably other natural processes, 
by taking out the superfluous phlogiston, restore it to its original purity. 
But I own I had no idea of the possibility of going any farther in this 
way, and thereby procuring air purer than the best common air. I might, 
indeed, have naturally imagined that such would be air that should 
contain less phlogiston than the air of the atmosphere; but I had no idea 
that such a composition was possible. [Here as throughout his life 
Priestley is using the concept of phlogiston to explain combustion and 

Priestley's First Experiments with Red Oxide of Mercury 

Publication of these results in Priestley's Experiments, as given below, 
followed the communication of three letters announcing the essential 

94 CASE 2 

facts to the Royal Society; they are dated March 15, April i, and May 
29, 1775, and were printed in volume 65 of the Philosophical Transac- 
tions of the Royal Society for that year, which seems to have appeared 
more promptly than the corresponding record of the French Academy. 

At the time of my former publication, I was not possessed of a burning 
lens of any considerable force; and for want of one, I could not possibly 
make many of the experiments that I had projected, and which, in 
theory, appeared very promising. I had, indeed, a mirror of force suffi- 
cient for my purpose. But the nature of this instrument is such, that it 
cannot be applied, with effect, except upon substances that are capable of 
being suspended, or resting on a very slender support. It cannot be 
directed at all upon any substance in the form of powder, nor hardly 
upon any thing that requires to be put into a vessel of quicksilver [liquid 
metallic mercury] ; which appears to me to be the most accurate method 
of extracting air from a great variety of substances, as was explained in 
the Introduction to this volume. But having afterwards procured a lens 
of twelve inches diameter, and twenty inches focal distance, I proceeded 
with great alacrity to examine, by the help of it, what kind of air a great 
variety of substances, natural and factitious, would yield, putting them 
into the vessels . . . which I filled with quicksilver, and kept inverted in 
a bason of the same. Mr. Warltire, a good chymist, and lecturer in 
natural philosophy, happening to be at that time in Calne, I explained 
my views to him, and was furnished by him with many substances, 
which I could not otherwise have procured. 

Priestley's statements about the mirror are at first sight somewhat 
perplexing. The point is not important, however. Apparently Priestley 
had a concave mirror enabling him to bring a beam of sunlight to a 
focus and thus concentrate the radiant energy. However, the material 
placed at the focus of a concave mirror is between the source of light 
and the reflecting surface. It must be small if it is not to cut off a large 
portion of the beam of light. With a lens there is, of course, no such 
difficulty (see Fig. 2). 

With this apparatus, after a variety of other experiments, an account 
of which will be found in its proper place, on the ist of August, 1774, 
I endeavoured to extract air from mercurius calcinatus per se; and I 
presently found that, by means of this lens, air was expelled from it very 
readily. [The gas evolved, which was oxygen, displaced the mercury.] 
Having got about three or four times as much as the bulk of my ma- 
terials, I admitted water to it, and found that it was not imbibed by it. 
[This showed that the gas was not carbon dioxide which he suspected 
would be formed.] But what surprized me more than I can well express, 
was, that a candle burned in this air with a remarkably vigorous flame, 
very much like that enlarged flame with which a candle burns in nitrous 
air, exposed to iron or liver of sulphur [calcium sulfide which, like iron, 



transforms nitric oxide into laughing gas (see p. 91); that is, Priestley 
thought he was dealing with what we now call laughing gas] ; but as I 
had got nothing like this remarkable appearance from any kind of air 
besides this particular modification of nitrous air [laughing gas], and 
I knew no nitrous acid was used in the preparation of mercurius cal- 
dnatus, I was utterly at a loss how to account for it. ["Nitrous air" re- 
quires a nitrate for its preparation and this in turn requires nitric acid 
or its equivalent. This acid was called nitrous acid in Priestley's day.] 

Burning lens 

Red oxide of mercury 

Liquid mercury 

Level of-* 
after heating 

FIG. 2. Priestley's method of heating red oxide of mercury with a burning lens. 

In this case, also, though I did not give sufficient attention to the 
circumstance at that time, the flame of the candle, besides being larger, 
burned with more splendor and heat than in that species of nitrous air 
[i.e., laughing gas]; and a piece of red-hot wood sparkled in it, exactly 
like paper dipped in a solution of 'nitre [potassium nitrate used in the 
manufacture of gunpowder], and it consumed very fast; an experiment 
which I had never thought of trying with nitrous air. [Priestley probably 
means here nitrous air modified by exposure to iron.] 

At the same time that I made the above-mentioned experiment, I 
extracted a quantity of air, with the very same property, from the com- 
mon red precipitate, which being produced by a solution of mercury in 
spirit of nitre [nitric acid], made me conclude that this peculiar property, 
being similar to that of the modification of nitrous air above mentioned, 
depended upon something being communicated to it by the nitrous acid 
[nitric acid]; and since the mercurius calcinatus is produced by exposing 
mercury to a certain degree of heat, where common air has access to it, 
I likewise concluded that this substance had collected something of nitre, 
in that state of heat, from the atmosphere [a not unlikely supposition but 
erroneous, for it is in fact the oxygen of the nitric acid that is left united 
with the mercury when the red oxide is prepared from the nitrate] . 

This, however, appearing to me much more extraordinary than it 
ought to have done, I entertained some suspicion that the mercurius 

96 CASE 2 

caicinatus, on which I had made my experiments, being bought at a 
common apothecary's, might, in fact, be nothing more than red precipi- 
tate; though, had I been any thing of a practical chymist, I could not 
have entertained any such suspicion. However, mentioning this suspicion 
to Mr. Warltire, he furnished me with some that he had kept for a 
specimen of the preparation, and which, he told me, he could warrant to 
be genuine. This being treated in the same manner as the former, only 
by a longer continuance of heat, I extracted much more air from it than 
from the other. 

This is an example o careful chemical experimentation. More than 
one chemist has gone astray by the wrong identification of his ma- 
terials. Red oxide prepared via mercury nitrate, that is, by dissolving 
mercury in nitric acid, evaporating, and heating the residue might be 
different from the red powder produced by heating mercury in air. 

This experiment might have satisfied any moderate skeptic: but, 
however, being at Paris in the October following, and knowing that 
there were several very eminent chymists in that place, I did not omit 
the opportunity, by means of my friend Mr. Magellan, to get an ounce 
of mercurius caicinatus prepared by Mr. Cadet, of the genuineness of 
which there could not possibly be any suspicion; and at the same time, 
I frequently mentioned my surprize at the kind of air which I had got 
from this preparation to Mr. Lavoisier, Mr. le Roy, and several other 
philosophers, who honoured me with their notice in that city; and who, 
I dare say, cannot fail to recollect the circumstance. 

By an interesting coincidence Lavoisier obtained his sample of red 
oxide of mercury from the same Parisian apothecary. The two samples 
may well have come from the same bottle. Priestley's conversation with 
Lavoisier has been the subject of much debate among historians of 
science. Since at this time he was inclined to think the gas in question 
was laughing gas, he could not have told Lavoisier of the discovery of 
a new gas. Yet the fact that the gas was not carbon dioxide ("fixed 
air") and that it did support combustion was an important fact to one 
who, like Lavoisier, was intent on solving the problem of combustion 
and calcination. The French chemist Bayen in February of the same 
year had published the erroneous statement that the red powder on 
heating alone gave fixed air. Bayen's work may have provided the 
stimulus for Lavoisier's examination of the behavior of red oxide of 
mercury on heating, but it is far more likely that it was Priestley's 
remarks to him. These were made in October; according to Lavoisier's 
own statement, he started his experiments in November. 

At the same time, I had no suspicion that the air which I had got 
from the mercurius caicinatus was even wholesome, so far was I from 


knowing what it was that I had really found; taking it for granted, that 
it was nothing more than such kind of air as I had brought nitrous air to 
be by the processes above mentioned; and in this air I have observed that 
a candle would burn sometimes quite naturally, and sometimes with a 
beautiful enlarged flame, and yet remain perfectly noxious. 

At the same time that I had got the air above mentioned from mer- 
curius calcinatus and the red precipitate, I had got the same kind from 
red lead or minium [a red oxide of lead]. In this process, that part of 
the minium on which the focus of the lens had fallen, turned yellow. 
One third of the air, in this experiment, was readily absorbed by water 
[due to some carbon dioxide from carbonate mixed with the oxide], but, 
in the remainder, a candle burned very strongly, and with a crackling 

That fixed air [carbon dioxide] is contained in red lead I had ob- 
served before; for I had expelled it by the heat of a candle, and had 
found it to be very pure. See Vol. I, p. 192. I imagine it requires more 
heat than I then used to expel any of the other kind of air. [This is 
correct; the carbonate decomposes easily. However, Priestley assumes 
that his red lead is a homogeneous substance. His sample clearly was 
not, but contained some lead carbonate. One of the advantages of 
mercury oxide for preparing oxygen is that unlike many other oxides it 
is not contaminated with carbonate by any method of preparation.] 

This experiment with red lead confirmed me more in my suspicion, 
that the mercurius calcinatus must get the property of yielding this kind 
of air from the atmosphere, the process by which that preparation, and 
this of red lead is made, being similar. As I never make the least secret 
of any thing that I observe, I mentioned this experiment also, as well as 
those with the mercurius calcinatus, and the red precipitate, to all rny 
philosophical acquaintance at Paris, and elsewhere; having no idea, at 
that time, to what these remarkable facts would lead. 

Presently after my return from abroad, I went to work upon the 
mercurius calcinatus, which I had procured from Mr. Cadet; and, with 
a very moderate degree of heat, I got from about one fourth of an ounce 
of it, an ounce-measure of air [the relation of weight to volume of air 
is of no particular significance], which I observed to be not readily im- 
bibed, either by the substance itself from which it had been expelled 
(for I suffered them to continue a long time together before I trans- 
ferred the air to any other place) or by water, in which I suffered this 
air to stand a considerable time before I made any experiment upon it. 

In this air, as I had expected, a candle burned with a vivid flame; but 
what I observed new at this time, (Nov. 19,) and which surprized me 
no less than the fact I had discovered before, was, that, whereas a few 
moments agitation in water will deprive the modified nitrous air of its 
property of admitting a candle to burn in it; yet, after more than ten 
times as much agitation as would be sufficient to produce this alteration 
in the nitrous air, no sensible change was produced in this. A candle 

98 CASE 2 

still burned in it with a strong flame. . . [The "nitrous air" here men- 
tioned is nitrous oxide or laughing gas which, as already stated, is soluble 
in water. Priestley's preparation of this gas from nitric oxide resulted in a 
mixture; agitation with water removed the nitrous oxide.] 

But I was much more surprized, when, after two days, in which this 
air had continued in contact with water (by which it was diminished 
about one twentieth of its bulk) I agitated it violently in water about 
five minutes, and found that a candle still burned in it as well as in 
common air. The same degree of agitation would have made phlogisti- 
cated nitrous air [laughing gas] fit for respiration indeed, but it would 
certainly have extinguished a candle [because most of the laughing gas 
would have been dissolved in the water; the difference in solubility of 
laughing gas and oxygen in water gave Priestley his first hint] . 

These facts fully convinced me, that there must be a very material 
difference between the constitution of the air from mercurius calcinatus, 
and that of phlogisticated nitrous air [laughing gas], notwithstanding 
their resemblance in some particulars. But though I did not doubt that 
the air from mercurius calcinatus was fit for respiration, after being 
agitated in water, as every kind of air without exception, on which I had 
tried the experiment, had been, I still did not suspect that it was respir- 
able in the first instance; so far was I from having any idea of this air 
being, what it really was, much superior, in this respect, to the air of the 

In this ignorance of the real nature of this kind of air, I continued 
from this time (November) to the ist of March following; having, in 
the mean time, been intent upon my experiments on the vitriolic acid air 
above recited, and the various modifications of air produced by spirit of 
nitre, an account of which will follow. [These experiments are not 
relevant.] But in the course of this month, I not only ascertained the 
nature of this kind of air, though very gradually, but was led by it to the 
complete discovery of the constitution of the air we breathe. 

Till this ist of March, 1775, I had so little suspicion of the air from 
mercurius calcinatus, &c, being wholesome, that I had not even thought 
of applying to it the test of nitrous air [on this point Lavoisier was 
quicker on the trigger, for he applied this test at once, though, as we have 
seen, with unfortunate results] ; but thinking (as my reader must imag- 
ine I frequently must have done) on the candle burning in it after long 
agitation in water, it occurred to me at last to make the experiment; and 
putting one measure of nitrous air to two measures of this air [the 
standard procedure devised by Priestley himself] , I found, not only that 
it was diminished, but that it was diminished quite as much as common 
air [Priestley misses the quantitative difference at this time; see the next 
paragraph], and that the redness of the mixture was likewise equal to 
that of a similar mixture of nitrous and common air. 

After this I had no doubt but that the air from mercurius calcinatus 
was fit for respiration, and that it had all the other properties of genuine 


common air. But I did not take notice of what I might have observed, if 
I had not been so fully possessed by the notion of there being no air 
better than common air, that the redness was really deeper, and the 
diminution something greater than common air would have admitted. 
[See p. 75 for explanation.] 

Moreover, this advance in the way of truth, in reality, threw me back 
into error, making me give up the hypothesis I had first formed, viz. 
that the mercurius calcinatus had extracted spirit of nitre from the air; 
for I now concluded, that all the constituent parts of the air were equally, 
and in their proper proportion, imbibed in the preparation of this sub- 
stance, and also in the process of making red lead. [As far as errors are 
concerned there is little to choose; both hypotheses, in fact, were wrong!] 
For at the same time that I made the above-mentioned experiment on 
the air from mercurius calcinatus, I likewise observed that the air which I 
had extracted from red lead, after the fixed air was washed out of it, was 
of the same nature, being diminished by nitrous air like common air: 
but, at the same time, I was puzzled to find that air from the red 
precipitate was diminished in the same manner, though the process for 
making this substance is quite different from that of making the two 
others. But to this circumstance I happened not to give much attention. 

I wish my reader be not quite tired with the frequent repetition of 
the word surprize, and others of similar import; but I must go on in that 
style a little longer. For the next day I was more surprized than ever I 
had been before, with finding that, after the above-mentioned mixture 
of nitrous air and the air from mercurius calcinatus, had stood all night, 
(in which time the whole diminution must have taken place; and, con- 
sequently, had it been common air, it must have been made perfectly 
noxious, and intirely unfit for respiration or inflammation [i.e., would 
have been nitrogen]) a candle burned in it, and even better than in 
common air. 

I cannot, at this distance of time, recollect what it was that I had in 
view in making this experiment; but I know I had no expectation of the 
real issue of it. Having acquired a considerable degree of readiness in 
making experiments of this kind, a very slight and evanescent motive 
would be sufficient to induce me to do it. If, however, I had not happened, 
for some other purpose, to have had a lighted candle before me, I should 
probably never have made the trial; and the whole train of my future 
experiments relating to this kind of air might have been prevented. 
[Priestley's critics have made much fun of this honest statement. Few 
experimenters are as frank about their lucky strikes.] 

Still, however, having no conception of the real cause of this phenome- 
non, I considered it as something very extraordinary; but as a property 
that was peculiar to air extracted from these substances, and adventi- 
tiousi and I always spoke of the air to my acquaintance as being substan- 
tially the same thing with common air. I particularly remember my 
telling Dr. Price, that I was myself perfectly satisfied of its being com- 

100 CASE 2 

mon air, as it appeared to be so by the test of nitrous air; though, for 
the satisfaction of others, I wanted a mouse to make the proof quite 

Up to this point, Priestley is just where Lavoisier was, and at about 
the same time. If he had published his results as they stood, he would 
have given the world conclusions almost identical with those that 
Lavoisier was then preparing to communicate to the Academy (Easter 


On the 8th of this month I procured a mouse, and put it into a glass 
vessel, containing two ounce-measures of the air from mercurius calci- 
natus. Had it been common air, a full-grown mouse, as this was, would 
have lived in it about a quarter of an hour. In this air, however, my 
mouse lived a full half hour; and though it was taken out seemingly 
dead, it appeared to have been only exceedingly chilled; for, upon being 
held to the fire, it presently revived, and appeared not to have received 
any harm from the experiment. 

By this I was confirmed in my conclusion, that the air extracted from 
mercurius calcinatus, &c. was, at least , as good as common air; but I did 
not certainly conclude that it was any better; because, though one mouse 
would live only a quarter of an hour in a given quantity of air, I knew 
it was not impossible but that another mouse might have lived in it half 
an hour; so little accuracy is there in this method of ascertaining the 
goodness of air: and indeed I have never had recourse to it for my own 
satisfaction, since the discovery of that most ready, accurate, and elegant 
test that nitrous air furnishes. [This is an example of sound and careful 
reasoning about the tactics of experimentation.] But in this case I had a 
view to publishing the most generally-satisfactory account of my experi- 
ments that the nature of the thing would admit of. 

This experiment with the mouse, when I had reflected upon it some 
time, gave me so much suspicion that the air into which I had put it was 
better than common air, that I was induced, the day after, to apply the 
test of nitrous air to a small part of that very quantity of air which the 
mouse had breathed so long; so that, had it been common air, I was 
satisfied it must have been very nearly, if not altogether, as noxious as 
possible, so as not to be affected by nitrous air; when, to my surprize 
again, I found that though it had been breathed so long, it was still 
better than common air. [Here we come near to the crucial point, the 
examination of a residual gas after a test. If common air was at hand, the 
exhaustion of the oxygen by the respiration of the mouse would have 
yielded an air whose goodness by the "nitrous air test" would have been 
low,] For after mixing it with nitrous air, in the usual proportion of 
two to one, it was diminished in the proportion of 4 1 / 2 to 3%; that is, 
the nitrous air had made it two ninths less than before, and this in a very 
short space of time; whereas I had never found that, in the longest 
time, any common air was reduced more than one fifth of its bulk by 


any proportion of nitrous air, nor more than one fourth by any phlogistic 
process whatever. [The difference between two ninths and one fifth (one 
forty-fifth) was beyond the limits of accuracy of Priestley's measure- 
ments. The greatest change in volume by absorption of all the oxygen 
by combustion (a phlogistic process) yields a diminution of one fifth 
only if the experiment is carefully performed.] Thinking of this extraor- 
dinary fact upon my pillow, the next morning I put another measure of 
nitrous air to the same mixture, and, to my utter astonishment, found 
that it was farther diminished to almost one half of its original quantity. 
I then put a third measure to it; but this did not diminish it any farther: 
but, however, left it one measure less than it was even after the mouse 
had been taken out of it. [Here is the crucial experiment.] 

Being now fully satisfied that this air, even after the mouse had 
breathed it half an hour, was much better than common air; and having 
a quantity of it still left, sufficient for the experiment, viz. an ounce- 
measure and a half, I put the mouse into it; when I observed that it 
seemed to feel no shock upon being put into it, evident signs of which 
would have been visible, if the air had not been very wholesome; but 
that it remained perfectly at its ease another full half hour, when I took 
it out quite lively and vigorous. Measuring the air the next day, I found 
it to be reduced from 1 1 / 2 to % of an ounce-measure. And after this, if I 
remember well (for in my register of the day I only find it noted, that it 
was considerably diminished by nitrous air) it was nearly as good as 
common air. It was evident, indeed, from the mouse having been taken 
out quite vigorous, that the air could not have been rendered very 

For my farther satisfaction I procured another mouse, and putting it 
into less than two ounce-measures of air extracted from mercurius calci- 
natus and air from red precipitate [red oxide prepared via nitric acid] 
(which, having found them to be of the same quality, I had mixed to- 
gether) it lived three quarters of an hour. But not having had the pre- 
caution to set the vessel in a warm place, I suspect that the mouse died 
of cold. However, as it had lived three times as long as it could probably 
have lived in the same quantity of common air, and I did not expect 
much accuracy from this kind of test, I did not think it necessary to make 
any more experiments with mice. 

Being now fully satisfied of the superior goodness of this kind of air, 
I proceeded to measure that degree of purity, with as much accuracy as 
I could, by the test of nitrous air; and I began with putting one measure 
of nitrous air to two measures of this air, as if I had been examining 
common air; and now I observed that the diminution was evidently 
greater than common air would have suffered by the same treatment. 
A second measure of nitrous air reduced it to two thirds of its original 
quantity, and a third measure to one half. Suspecting that the diminution 
could not proceed much farther, I then added only half a measure of 
nitrous air, by which it was diminished still more; but not much, and 

m CASE 2 

another half measure made it more than half of its original quantity; so 
that, in this case, two measures of this air took more than two measures 
of nitrous air, and yet remained less than half of what it was. Five meas- 
ures brought it pretty exactly to its original dimensions. [It is assumed 
that the experiments are carried out over water, of course.] 

At the same time, air from the red precipitate was diminished in the 
same proportion as that from mercurius calcinatus, five measures of 
nitrous air being received by two measures of this without any increase 
of dimensions. Now as common air takes about one half of its bulk of 
nitrous air, before it begins to receive any addition to its dimensions 
from more nitrous air, and this air took more than four half-measures 
before it ceased to be diminished by more nitrous air, and even five half- 
measures made no addition to its original dimensions, I conclude that it 
was between four and five times as good as common air. It will be seen 
that I have since procured air better than this, even between five and 
six times as good as the best common air that I have ever met with. 

These two paragraphs record the convincing experiments which 
showed that the gas at hand was not common air but a new substance. 
Pure "nitrous air" and pure oxygen when brought together over water 
combine in about the ratio of 2 to i; the exact relation depends on the 
way the experiment is performed and the temperature. Priestley's 
results are the equivalent of a reaction between about 4 half measures 
or 2 volumes of nitrous air and i volume of oxygen. This indicates that 
his gases were quite pure. The final residual gas was the excess of 
nitrous air which was used. If he had used smaller increments he might 
have had almost no residue after the proper amount of nitrous air had 
been added over water. The effective discovery of oxygen by Priestley 
may be considered to have taken place when these experiments were 
made and interpreted. 

Being now fully satisfied with respect to the nature of this new species 
of air, viz. that, being capable of taking more phlogiston from nitrous 
air, it therefore originally contains less of this principle [a consistent 
use of the phlogiston terminology]; my next inquiry was, by what 
means it comes to be so pure, or philosophically speaking, to be so much 
dephlogisticated\ and since the red lead yields the same kind of air with 
mercurius calcinatus, though mixed with common air, and is a much 
cheaper material, I proceeded to examine all the preparations of lead, 
made by heat in the open air, to see what kind of air they would yield, 
beginning with the grey calx, and ending with litharge. 

The red lead which I used for this purpose yielded a considerable 
quantity of dephlogisticated air, and very little fixed air; but to what 
circumstance in the preparation of this lead, or in the keeping of it, this 
difference is owing, I cannot tell. I have frequently found a very remark- 
able difference between different specimens of red lead in this respect, 


as well as in the purity of the air which they contain. [Here Priestley 
practically admits that his samples of red lead were not homogeneous, 
but neither then nor subsequently does he draw the correct conclusion. 
This is another illustration of the difficulties of correct interpretation of 
chemical "facts."] This difference, however, may arise in a great measure, 
from the care that is taken to extract the fixed air from it. In this ex- 
periment two measures of nitrous air being put to one measure of this 
air, reduced it to one third of what it was at first, and nearly three times 
its bulk of nitrous air made very little addition to its original dimen- 
sions; so that this air was exceedingly pure, and better than any that 1 
had procured before. 

Then there follows in Priestley's volume an account of many experi- 
ments with the oxides of lead. Of these there are a number containing, 
as we now know, different ratios of oxygen and lead atoms. They have 
different colors which serve to distinguish them from each other. As 
prepared by the various methods known to Priestley, they often con- 
tained not only a mixture of lead oxides but also lead carbonate and 
lead nitrate (if nitric acid was used in their preparation). Probably 
most, if not all, the oxygen that Priestley obtained from them came 
from the decomposition of the lead nitrate, for nitrates on heating fre- 
quently yield oxygen, an oxide of nitrogen, and an oxide of the metal. 
We need not pursue Priestley's investigation of these complications 
further except to note that he was led farther and farther from the 
right road by these subsequent inquiries. He began to confuse nitrates 
and carbonates and oxides and consequently developed the idea that a 
calx had imbibed "spirit of nitre," that is, nitric acid, from the air. Not 
having any adequate criteria of purity and not operating with constant 
regard for changes in weight and in volume, he proceeded from one 
faulty experiment to another. We need not follow his further work 
on calces, for he never arrived at a final conclusion. But he always had 
at his disposal some alleged fact, such as the statement that "some 
metallic calces yield fixed air on heating," to challenge Lavoisier's 
conceptual scheme and support the phlogiston theory. For the student 
of the history of the development of science, the importance of this part 
of the story, thus briefly summarized, is as follows: homogeneity of 
materials is as essential to the chemist as the control of such variables 
as temperature and pressure is to the physicist; furthermore, criteria 
for determining homogeneity are often extremely difficult to establish, 
and it was only slowly that such criteria were evolved. Only after 
Lavoisier's "principle of the balance sheet" became accepted among 
chemists could such criteria be found for many materials. A complete 
quantitative study of the decomposition by heat of various samples of 
red lead, for example, with and without the addition of charcoal, wiU 

104 CASE 2 

yield the necessary information to tell the investigator whether two 
samples are identical in composition and whether carbonate or nitrate 
is also present. 


A study of the accounts by Lavoisier and Priestley of their first 
experiments with oxygen illustrates a number of general principles in 
the development of science. First, a contrast of the method of publish- 
ing the results and the reference to other works with early seventeenth- 
century practice on the one hand and twentieth-century procedure on 
the other, illustrates the growth of science as an organized activity. 
Second, the difficulties of chemical experimentation are exposed very 
clearly; the difficulties are sometimes those of interpretation of what 
is observed, sometimes the failure to try what now seems an obvious 
further experiment, often the failure to have homogeneous materials at 
hand. Third, the role of the accidental discovery is almost glorified by 
Priestley. Fourth, repeated use of the limited working hypothesis is 
evident. For example, every time a chemical test is applied, Priestley or 
Lavoisier is essentially saying, "If I do so and so, such and such will 
happen." Priestley's original faulty identification of oxygen as laughing 
gas and his failure to interpret the "nitrous air test" correctly shows 
how many hidden assumptions are involved in the interpretation of 
experimental results. Fifth, Priestley's blind adherence to the phlogiston 
theory in spite of his own effective discovery of oxygen and in spite 
of its obvious faults (such as the failure to account for the increase in 
weight on calcination) shows the hold that one conceptual scheme may 
have on the mind of an investigator. Sixth y the transformation of a 
broad working hypothesis into a new conceptual scheme is made evi- 
dent by following Lavoisier's work. His broad working hypothesis was 
by 1778 well on its way to becoming a new conceptual scheme of revo- 
lutionary importance. 

Long before Priestley and Lavoisier, the increase in weight of metals 
on calcination was recorded and at least one investigator had come 
close to an effective discovery of oxygen. Priestley's emphasis on the 
accidental nature of scientific discoveries should not deceive the reader 
into believing that scientific progress hangs on such accidents, nor 
should Lavoisier's brilliance lead one to conclude that science is solely 
the work of a few great men. Among the complex of conditions which 
determined that in the late eighteenth rather than in the late seven- 
teenth century the time was ripe for an elucidation of combustion we 
may list the following: (a) the improvement in communications 
among scientific men, which made science more and more of a co- 


operative effort; (b} the accumulation of quantitative studies in physics 
that made unsatisfactory the concept of phlogiston, which implied a 
substance with a negative weight; (c) the accumulation of a century's 
work on the materials, apparatus, and techniques of chemistry. 


The discovery of oxygen was the central event in the over- 
throw of the phlogiston theory. But it must be remembered that it was 
the discovery that oxygen was a constituent of the atmosphere which 
provided the key to the riddle of combustion. The method of preparing 
the red oxide of mercury was an essential link in Lavoisier's argument, 
He was at some pains in his Easter Memoir to show that the red 
powder was a true calx; it was formed when mercury was heated in 
air. In this process the gain in weight was due to combination of 
either air or a constituent of air with the mercury. By 1777 Lavoisier 
was clear that the principle that combined with metals during calcina- 
tion was "an eminently respirable air" which constituted only a part 
of common air. In his textbook, Traite ~lementaire de Chimie (Ele- 
ments of Chemistry), published in 1789, he describes an experiment 
which taken together with the preparation of oxygen from the red 
oxide demonstrates the composition of the atmosphere by analysis. The 
following extract is from an English translation of this book by 
Robert Kerr (London, ed. 5, 1802), modernized by the editor of this 

Lavoisier's Elements of Chemistry, Chapter III 

It appears that our atmosphere is composed of a mixture of substances 
capable of retaining the gaseous state at common temperatures, and 
under the usual degrees of pressure. These gases constitute a mass, in 
some measure homogeneous, extending from the surface of the earth to 
the greatest height hitherto attained, of which the density continually 
decreases in the inverse ratio of the superincumbent weight. . . . 

It is our business to endeavor to determine, by experiments, the nature 
of the elastic fluids which compose the lower stratum of air which we 
inhabit. Modern chemistry has made great advances in this research; and 
it will appear, by the following details, that the analysis of atmospherical 
air has been more rigorously determined than that of any other substance 
of the class. 

Chemistry affords two general methods of determining the constituent 
principles of bodies, the method of analysis, and that of synthesis. When, 
for instance, by combining water with alcohol, we form the species of 
liquor called, in commercial language, brandy, or spirit of wine, we 
certainly have a right to conclude, that brandy, or spirit of wine, is com- 



posed of alcohol combined with water. We can procure the same result 
by the analytical method; and in general it ought to be considered as a 
principle in chemical science, never to rest satisfied without both these 
species of proofs. We have this advantage in the analysis of atmospherical 
air; being able both to decompound it, and to form it anew in the most 
satisfactory manner. I shall, however, at present confine myself to re- 
count such experiments as are most conclusive upon this head; and I 
may consider most of these as my own, having either first invented 
them, or having repeated those of others, intended for analyzing at- 
mospherical air, in perfectly new points of view. 

I took a flask of about 36 cubical inches capacity, having a long neck 
bent as shown in the figure [Fig. 3] and placed in the furnace in such a 
manner that the extremity of its neck might be inserted under a bell- 


Liquid mercury 

(a red 



forms on 



Level of liquid 
after heating* 

Water or 

mercury for 

containing air 

FIG. 3. Boiling mercury absorbs oxygen from the air. 

glass, placed in a trough of quicksilver. I introduced four ounces of pure 
mercury into the flask and by means of a siphon, exhausted the air in the 
receiver so as to raise the quicksilver, and I carefully marked the height 
at which it stood, by pasting on a slip of paper. Having accurately noted 
the height of the thermometer and barometer, I lighted a fire in the 
furnace which I kept up almost continually during twelve days, so as to 
keep the quicksilver always very near its boiling point. Nothing re- 
markable took place during the first day: The mercury, though not 
boiling, was continually evaporating, and covered the interior surface of 
the vessel with small drops, which gradually augmenting to a sufficient 
size, fell back into the mass at the bottom of the vessel. On the second 
day, small red particles began to appear on the surface of the mercury; 
these, during the four or five following days, gradually increased in size 
and number, after which they ceased to increase in either respect. At the 
end of twelve days, feeling that the calcination of the mercury did not 
at all increase, I extinguished the fire, and allowed the vessels to cool. 


The bulk of air in the body and neck of the flask and in the bell-glass, 
reduced to a medium of 28 inches of the barometer and 54.5 of the 
thermometer, at the commencement of the experiment was about 50 
cubical inches. At the end of the experiment the remaining air, reduced 
to the same medium pressure and temperature, was only between 42 
and 43 cubical inches; consequently it had lost about 1/6 of its bulk. 
Afterwards, having collected all the red particles, formed Juring the 
experiment, from the running mercury in which they floated, I found 
these to amount to 45 grains. 

I was obliged to repeat this experiment several times, as it is difficult, 
in one experiment, both to preserve the whole air upon which we oper- 
ate, and to collect the whole of the red particles, or calx of mercury, 
which is formed during the calcination. . . . 

The air which remained after the calcination of the mercury in this 
experiment, and which was reduced to 5/6 of its former bulk, was no 
longer fit either for respiration or for combustion: animals being intro- 
duced into it were suffocated in a few seconds, and when a taper was 
plunged into it, it was extinguished, as if it had been immersed in water. 

This gas was commonly called "mephitic air." Lavoisier named it 
azote; in English the name nitrogen was introduced at this time. 

Lavoisier then describes the famous experiment of the Easter Memoir 
but uses only the 45 grains of red oxide prepared in the preceding 
experiment. From this he obtains 7 to 8 cubic inches of gas and 41.5 
grains of mercury. It is interesting to compare this result with those 
reported in 1775. The weight of the gas by difference is 3.5 grains, 
which gives a weight per cubic inch of about 0.5 or 0.44 grain (3.5 
divided by 7 or 8) . This figure is to be compared with the nearly 2/3 
reported earlier (p. 82). At this point an analysis of the atmospheric 
air had been accomplished. By the aid of mercury, a furnace, and other 
equipment, 50 cubic inches of air had been separated into 42 to 43 
cubic inches o air unfit for respiration or combustion (nitrogen) and 
7 to 8 cubic inches of oxygen. 

Lavoisier at this point draws the attention of the reader to the con- 
clusion "that atmospheric air is composed o two elastic fluids (gases) 
of different and opposite qualities." He further adds, "As a proof of 
this important truth, i we recombine these two elastic fluids which we 
have separately obtained in the above experiment, viz. the 42 cubical 
inches of mephitic air [nitrogen] with the 8 cubical inches of highly 
respirable air, we reproduce an air precisely similar to that of the 
atmosphere, and possessing nearly the same power of supporting com- 
bustion and respiration, and of contributing to the calcination of 
metals." This is proof by synthesis as Lavoisier used the word in his 
book. Since air is a mixture and not a chemical compound, some 

108 CASE 2 

chemists today would not speak of synthesizing air by mixing nitrogen 
and oxygen, for we generally reserve the word synthesis for the prepa- 
ration of a chemical compound. 

Lavoisier in the same chapter speaks of the "mutual adhesion of the 
two constituent parts of the atmosphere for each other." He thus seems 
to have something in the nature of a chemical compound in mind. 
And elsewhere he says that the method of analysis using boiling mer- 
cury is not accurate, for "the attraction of mercury to its respirable 
part of the air or rather to its base (i.e. 5 the gas deprived of caloric 
fluid) is not sufficiently strong to overcome all the circumstances which 
oppose this union ... In consequence, when the calcination ends, or 
is at least carried as far as is possible in a determinate quantity of 
atmospheric air, there still remains a portion of respirable air united 
to the mephitic air which the mercury cannot separate." These state- 
ments indicate that Lavoisier's picture of the atmosphere was some- 
what different from what we have today. Yet we must recall that in 
the third paragraph of his Chapter III (see p. 105) he refers to mixing 
water and alcohol when speaking of a synthesis. The distinction be- 
tween a mixture and a chemical compound was not yet quite clear. 
Only by the assiduous use of the "principle of the balance sheet" by 
hard-working investigators in the next two decades was it finally 
shown that elements unite in definite proportions to form a compound. 
A mixture, on the other hand, is characterized by the fact that a little 
more or less of one component will not greatly alter the properties, as 
in the case of mixtures of oxygen and nitrogen. Other criteria, of which 
Lavoisier was unaware, were later developed for distinguishing be- 
tween mixtures and compounds. 

Lavoisier was quite right about the difficulties of his method of 
analysis. However, the value he obtained of 16 parts by volume of 
oxygen and 84 of nitrogen is wrong. Dry air is composed of 21 percent 
of oxygen by volume, 78 percent of nitrogen, nearly i percent of 
the rare gases, and less than 0.05 percent of carbon dioxide. (The 
amount of moisture present depends on the temperature and the rela- 
tive humidity. At room temperature the maximum amount of water 
by volume that can be present is a little over 2 percent. Therefore, the 
minimum value for the oxygen content in a sample of common air 
taken without drying, as Lavoisier did, would be about 20.5 percent 
by volume.) Accurate methods of determining the composition of air 
were developed shortly after Lavoisier's first experiments and were 
improved in the following century. In principle they are identical with 
his method but a chemical substance is employed (usually in solution) 
that will rapidly combine with the oxygen present at room tempera- 


cure. The change in volume, as in Lavoisier's experiment, is a measure 

of the oxygen present. 


Although Lavoisier's new conceptual scheme was clearly 
developed and well buttressed by experiments by 1778, he did not 
attack the prevailing doctrine directly until 1783. In that year the 
French chemist published his Reflections on Phlogiston, which 
marshaled the evidence for the new ideas and showed that the concept 
of phlogiston was not only unnecessary but self -contradictory. At just 
this time the composition of water was established by experiments of 
Henry Cavendish (1731-1810) which were immediately repeated by 
Lavoisier. Priestley had once again started a series of important experi- 
ments but had not in this case carried through to even a correct 
qualitative conclusion. Historians of chemistry still argue over who is 
entitled to the credit for the highly important discovery that water is 
composed of oxygen and hydrogen in the proportions by weight of 
approximately 8 to i. Priestley, Cavendish, Lavoisier, and James Watt 
of steam-engine fame, are all contenders for the honor. 

With the discovery that water was formed when hydrogen was 
burned in air, Lavoisier's scheme was complete. Water was clearly the 
oxide of hydrogen. Lavoisier at once proceeded to test an obvious de- 
duction from this extension of his conceptual scheme, namely, that 
steam heated with a metal should yield a calx and hydrogen. It did. 
(The converse was likewise demonstrated at about the same time.) 

Hydrogen + Oxygen Water 
Steam heated with metal - Calx + Hydrogen 


These facts about the relation of water, hydrogen, oxygen, metals, 
and oxides would seem to leave no ground for the supporters o the 
phlogiston theory to stand on. But for a few years the new knowledge 
had the contrary effect. The believers in phlogiston were at last able to 
explain why a calx weighed more than the metal. This they did by a 
modification of the phlogiston theory which is illustrated by the follow- 
ing table: 

110 CASE 2 

Modified Phlogiston Theory 
(about 1785) 

Hydrogen = phlogiston (often carrying water) ; 

Oxygen = dephlogisticated air; 

Water = dephlogisticated air + phlogiston; 

Nitrogen = completely phlogisticated air; 

Common air = partially phlogisticated air carrying water; 

Metal = calx + phlogiston water; 

Calx = the base of a pure earth + water; 

Charcoal = phlogiston + ash + water. 

If one studies this table it becomes clear that a fairly satisfactory 
account can be given of the simple chemical reactions. Thus in calcina- 
tion the following process took place: 

Metal heated in air - Phlogisticated air + Calx (water absorbed 
from the air) . 

The metal lost phlogiston to the air, which would mean a loss in 
weight, but the resulting "base of the pure earth" absorbed water from 
the air and the consequent gain in weight more than offset the loss in 
weight due to the loss of phlogiston! 

The classic experiment with red oxide of mercury was formulated 
somewhat as follows: red oxide is a simple substance containing water; 
on heating, the phlogiston of the water combines with the simple 
substance (the pure earth) yielding the metal, while the rest of the 
water (dephlogisticated air) comes off and is collected. When mercury 
is heated in oxygen, the reverse process occurs; the phlogiston com- 
bines with the dephlogisticated air, forming water, which unites with 
the simple substance to form the calx. 

Henry Cavendish, one of the great scientific figures of the period 
(though a most eccentric gentleman) , was for a time an adherent of 
the modified phlogiston theory. In a famous article published in 1784 
(in the Philosophical Transactions of the Royal Society, Vol. 74) he 
summarizes Lavoisier's new ideas quite fairly and then writes (pp. 151- 

"It seems, therefore, from what has been said, as if the phenomena 
of nature might be explained very well on this [i.e., Lavoisier's] 
principle without the help of phlogiston; and indeed, as adding dc- 
phlogisticated air to a body comes to the same thing as depriving it 
of its phlogiston and adding water to it, and as there are, perhaps, no 
bodies entirely destitute of water, and as I 'know no way by which 
phlogiston can be transferred from one body to another, without leav- 


ing it uncertain whether water is not at the same time transferred, it 
will be very difficult to determine by experiment which of these opin- 
ions is the truest; but as the commonly received principle o phlogiston 
explains all phenomena at least as well as Mr. Lavoisier's, I have ad- 
hered to that" [italics by the editor of this Case] . 

In retrospect, we can see that the adherents to the modified phlogiston 
theory were fighting a rear-guard action. Before Lavoisier's execution 
by the revolutionary tribunal in 1794, many chemists had come to 
accept his views. By the end of the century Priestley was almost alone 
in defending the doctrine of phlogiston. The story of the last days of 
the phlogiston theory is of interest, however, in illustrating a recurring 
pattern in the history of science. It is often possible by adding a num- 
ber of new special auxiliary postulates to a conceptual scheme to save 
the theory at least temporarily. Sometimes, so modified, the con- 
ceptual scheme has a long life and is very fruitful; sometimes, as in the 
case of the phlogiston theory after 1785, so many new assumptions have 
to be added year by year that the structure collapses. Most of the illus- 
trations of this pattern, it should be pointed out, concern concepts and 
conceptual schemes of far less breadth than the phlogiston doctrine. 
They may be ideas that are useful in formulating merely some rela- 
tively narrow segment of physics, chemistry, astronomy, or experi- 
mental biology. What has just been said applies none the less. 

The publication of Lavoisier's Traite Elementaire de Chimie t with 
his exposition of the evidence in support of the new views and his new 
nomenclature, made the destruction of the phlogiston theory inevitable. 


The period 1770-1800 was a time of revolutions. The fact 
that the chemical revolution was contemporary with the American 
Revolution and preceded the French Revolution by a few years adds 
interest to the story. Priestley and Lavoisier were both involved in the 
French Revolution, the latter losing his life at the height of the terror, 
the former being driven from England because of his sympathies with 
the French revolutionists. During the same period the iron and steel 
industry was undergoing a major transformation that was the key to a 
series of events often called the industrial revolution of the late 
eighteenth century. The interconnections between these revolutions 
scientific, industrial, political, and social while many, are far from 
simple. A study of the lives of Priestley, Lavoisier, and Watt gives one 
a good picture of the status of scientific activity in this period. The 
important scientists are still for the most part amateurs, as they were 

112 CASE 2 

in the days of Robert Boyle (mid-seventeenth century) . Not until after 
the Napoleonic wars were the major contributions to the advance of 
chemistry (or physics) to come from the laboratories of the universi- 
ties. The importance of the Royal Society and the French Academy as 
media of communication of scientific information is evident to all who 
have read the preceding section on the effective discovery of oxygen. 

For those who are interested in the relation of science to technology, 
a study of the period in question will prove profitable. The advance in 
science and the progress in the practical arts are both rapid; yet the two 
borrow relatively little from each other in the way of concepts or new 
factual information. The cross connections are more evident than a 
century earlier and both activities have increased in importance since 
the seventeenth century. The application of science to industry, how- 
ever, still lies in the future. One must not be misled by coincidences in 
time and place. For example, it is important to remember that the 
whole revolution of the making of iron and steel in the eighteenth 
century was based on purely empirical experimentation. The substitu- 
tion of coke for charcoal, the invention of the crucible steel process, the 
improvements in iron-ore smelting that yielded pig iron, the develop- 
ment of the puddling process for making malleable iron (mild steel) 
were all accomplished without benefit of science. Not until after all 
these technical advances had been made did the impact of Lavoisier's 
new ideas enable people to recognize that the fundamental chemical 
distinction between iron and steel lay in the carbon content. The cut- 
and-try methods of practical men were for the time being far more 
effective in producing practical effects than the work of scientists. 

The progress in the manufacture of all manner of products in this 
period made men alert to the possibilities of employing scientific dis- 
coveries. An improved process for manufacturing sulfuric acid yielded 
a material useful in the textile industry; James Watt recognized (1785) 
the possibilities of using chlorine gas (then recently discovered) in 
bleaching textiles. Pharmacists in this period were keenly interested in 
chemical developments and prepared chemicals for the use not only of 
doctors but of those interested in experimentation. The story of 
Cadet's red oxide of mercury (p. 96) is a case in point. One would like 
to know when yellow phosphorus first became available to a pur- 
chaser, for after its discovery in the seventeenth century its manufac- 
ture was more or less of a secret and each investigator had to prepare 
his own material But Lavoisier in 1772 was able to purchase the 
theretofore rare substance. (The availability of new materials has often 
played an important role in the advance of chemistry; radioactive 
isotopes, which became readily available in the late 1940'$, have stimu- 
lated a vast amount of work.) Scientists and inventors were in com- 


munication in this period and willingly learned from one another. 
However, the theoretical framework of physics and chemistry was so 
meager that the advances in science, except for mechanics, made little 
impact on the practical arts. Another fifty to seventy-five years of 
scientific work would be required before the applications of science 
were of prime importance. 

The following chronological table may be of interest as a method of 
relating the various late-eighteenth-century revolutions to one another. 

1760 George II dies; accession of George III. 
1760 Smcaton improves blast furnaces for producing cast iron. 
1760 Bridgewater canal completed; halves cost of coal in Manchester. 
1760 Factory system and use of water-driven machinery firmly estab- 
lished in English silk industry. 

1764 Hargreaves' spinning jenny introduced into English textile in- 

1765 Stamp Act. 

1766 Cavendish (London) isolates and describes hydrogen gas (in- 
flammable air). 

1769 Watt's first steam engine. Arkwright greatly improves water- 
powered machines for textile industry. 

1772 Lavoisier's experiments with sulfur and phosphorus. Priestley 
publishes his nitrous air test for the "goodness" of air. 

1774 Death of Louis XV. 

1775 Lavoisier's "Easter Memoir" on calcination. Priestley's effective 
discovery of oxygen. 

1776 Declaration of American Independence. 

1776 Publication of Adam Smith's Wealth of Nations. 

1778 Lavoisier's revised memoir on calcination. 

1779 Further improvements in textile machinery in England. 
1781 Capitulation of British at Yorktown. 

1782-1783 Composition of water established; spread of Lavoisier's 
ideas; last stand of phlogiston theory. 

1783 Lavoisier and Laplace determine large number of specific heats. 

1784 Cort's puddling process for making malleable iron from cast 
iron using coal as fuel. 

1783 Peace between Great Britain and the United States. 

1784 Watt's improved steam engine. 

114 CASE 2 

1786 Watt brings to England from France news of Berthollet's 
process for bleaching by the action of chlorine (then believed to 
be a compound); this knowledge utilized by English textile 

1787 Constitutional convention at Philadelphia. 

1789 Publication of Lavoisier's Traite Elementaire dc Chimic setting 
forth results of the chemical revolution in clear and systematic 

1789 Louis XVI summons the States General (January) ; third estate 
adopts title of National Assembly; fall of the Bastille (July). 

1791 Birmingham mob burns Priestley's house. 

1792 Attack on the Tuileries, Louis XVI a prisoner; French Republic 

1793 Louis XVI executed; Committee of Public Safety in Paris; 
"Terror" in France begins. 

1793 War between Great Britain and France, continues with only 
short truces until 1815. 

1794 Execution of Lavoisier (May 8) ; fall and death of Robespierre 
(July) ; end of Terror. 

1796 Production of cast iron in Great Britain 125,000 tons, double the 

figure of a decade earlier. 
1798 Battle of the Nile. Nelson's victory assures supremacy of British 


1798 Publication of Essay on Population by Malthus. 

1799 Napoleon becomes First Consul. 

1. Books Directly Related to the Effective Discovery of Oxygen 

Torch and Crucible, The Life and Death of Antoine Lavoisier, by 
Sidney J. French (Princeton University Press, 1941). A popular account of 
Lavoisier's work; combination of a biography and exposition of the chemi- 
cal revolution. Recommended for students of this Case. 

Three Philosophers (Lavoisier, Priestley, and Cavendish), by W. R. 
Aykroyd (London, 1935; out of print). 

Anioine Lavoisier, by Douglas McKie (Philadelphia, 1935; out of print). 

The Eighteenth Century Revolution in Science: The First Phase, by A. U. 
Meldrum (Calcutta: Longmans, Green, 1930). This pamphlet, which is 
difficult to obtain, is an authoritative scholarly review of the work of 
Lavoisier and Priestley. 


Elements of Chemistry, by Antoine Lavoisier (English translation by 
Robert Kerr, 1793; many editions). The first four or five chapters can be 
read with profit by students of this Case. 

Historical Introduction to Chemistry, by T. M. Lowry (London: Mac- 
millan, 1936). A good guide to those interested in an elementary presenta- 
tion of any phase of the history of chemistry since 1700. 

Lectures on Combustion, by Joseph Priestley and John MacLean, edited 
by William Foster (Princeton University Press, 1929). Throws interesting 
light on Priestley's last stand in defense of the phlogiston theory. 

2. The Eighteenth-Century Background 

Among the vast number of books dealing with the political and social 
history of the last half of the eighteenth century, the following may have 
special relevance for the student of this Case. 

Life of Joseph Priestley, by Anne Holt (Oxford, 1931). 

The Eighteenth Century Background, by Basil Willey (London, 1940). 
Chapter X on Priestley is recommended. 

Science and Social Welfare in the Age of Newton, by G. N. Clark (Ox- 
ford: Clarendon Press, 1937). Although this little volume deals with an 
earlier period, it is recommended for students of this Case as providing a 
picture of the economic and cultural factors involved in the interaction of 
science and technology. 

Iron and Steel in the Industrial Revolution, by T. S. Ashton (1924). 
Too detailed and technical for the average student, but contains a great 
deal of interesting material. 


The Early Development 
of the Concepts of 
Temperature and Heat 

The Rise and Decline of 
the Caloric Theory 




The of the 

of Temperature 


The development of thermometry, of methods for measuring 
heat, and of concepts about the nature of heat in the seventeenth and 
eighteenth centuries can be understood with little or no previous knowl- 
edge about science. The reason is that the growth of thermal science 
constitutes an epoch in scientific history that occurred almost independ- 
ently of basic developments in other parts of experimental science. 
Nevertheless, because these early developments in thermal science were 
far from being superficial in character, one can gain from the study of 
them a rather deep insight into the ways in which a fundamental, 
though limited, body of scientific knowledge came into being. 

As the present Case History will show, quantitative studies of phe- 
nomena connected with heat became possible only after the invention 
of the thermometer. Section i is a brief outline of important steps in 
the early development of this instrument, which will give the reader 
an appreciation of the difficulties that are likely to be encountered in 
the development of a satisfactory measuring instrument, and will also 
enable him to formulate for himself some general principles applicable 
to many instruments of this class. 

Section 2, which is based on excerpts from the published lectures of 
Joseph Black, shows how the thermometer made possible new concepts 
of fundamental importance, and how it led in turn to the invention of 
a new type of thermal instrument the calorimeter. Here the reader 
may be able to decide whether Sir Humphry Davy (Sec. 5) was correct 
in an assertion which he once made that "nothing tends so much to the 
advancement of knowledge as the application of a new instrument." 

Speculations current during the sixteenth and seventeenth centuries 
on the nature of heat had little effect on thermometry and the measure- 
ment of heat. However, Black described various views (Sec. 2), and the 
last three sections of this Case History describe how the most useful of 
these eighteenth-century conceptual schemes the caloric theory 

120 CASE 3 

was subjected to experimental tests by Count Rumford and by Davy, 
and make clear the role o their experiments in weakening the founda- 
tions of that theory. 

The final downfall of the caloric theory and the subsequent correlation 
of the sciences of heat and mechanics did not occur until near the middle 
of the nineteenth century and is not treated in detail here. But the reader 
will be able to see how, from thermometry through heat measure- 
ments to early speculations about what heat is, the thread of scientific 
history here followed finally led to the development of the modern 
theory of heat as a mode of motion. It also led to the enunciation of one 
of the great generalizations of physical science the principle of con- 
servation of energy. 


The earliest forms of the thermometer appear to have been sug- 
gested by a sixteenth-century revival of interest in various mechanical 
devices and toys invented during the Hellenic period, particularly by 
Philo of Byzantium and Hero of Alexandria. Certain of these ancient 
devices depended for their operation upon fhe expansion of air when 
heated. But the idea of adapting them to the purpose of indicating 
"degrees of hotness," or temperature, seemingly occurred to no one in 
ancient or medieval times. 

Galileo's barothermoscope ', ca. 1592-1603. Although it is not known 
with certainty who first conceived the idea of trying to measure tempera- 
tures, the adaptation of the ancient devices to this purpose is generally 
attributed to Galileo Galilei. He seems not to have appreciated the in- 
vention, for his own writings, so far as they have survived, contain only 
one incidental reference to the principle of the instrument. However, 
records left by several of his friends and students indicate that he de- 
vised and used it shortly after 1592. 

The instrument was merely a glass bulb containing air and having 
a long stem which extended downward into a vessel of water. As the 
temperature changed, the air in the bulb expanded or contracted and 
the water in. the stem fell or rose. Thus air was the temperature-indicat- 
ing substance, and its expansion served as the temperature-indicating 
property. Galileo appears also to have added to the device a scale, which 
probably consisted of a long narrow strip of paper attached to the stem 
and marked off in degrees "at pleasure." One such scale was divided 
into eight large spaces, and each of these into 60 smaller ones, a scheme 
possibly suggested by the graduation of astronomical instruments into 
degrees and minutes. 


Since there was no thought of basing these scales on standard, repro- 
ducible temperatures, the temperature indications were at best only 
semiquantitative. Thus Galileo's instrument is usually referred to as a 
thermoscope, a term that first came into use in 1617, rather than as a 
thermometer, a term that was not coined until 1624. More accurately 
speaking, his instrument was a "barotheraioscope," for it indicated 
changes in atmospheric pressure as well as temperature; but this fact 
apparently was not clearly recognized until some time after the inven- 
tion of the barometer (1643). 

One of Galileo's colleagues, Sanctorius, who was professor of medi- 
cine at the University of Padua, applied Galileo's barothermoscope to 
the detection of fevers and other physiologic studies. Recognizing that 
fiducial points are needed for a satisfactory measuring device, Sanctorius 
made marks on his scale to indicate the two readings obtained when the 
bulb of the instrument was exposed, first to snow, and then to the flame 
of a candle. 

First liquid-expansion thermoscope s t 1632-1641. The expansion of a 
liquid was probably first employed for estimating temperatures by Jean 
Key, a French physician, in 1631. His instrument, which he used for 
taking the temperature of patients, was a glass bulb and stem similar 
to Galileo's, except that it was inverted and partly filled with water. 
The upper end of the stem was left open, so the readings were influ- 
enced by evaporation of the water, although not to an appreciable extent 
by changes in atmospheric pressure. 

The first thermoscope with the end of the stem sealed, and also utiliz- 
ing the expansion of alcohol instead of water (Plate I, i, 2), was devel- 
oped in 1641 by the Grand Duke Ferdinand II of Tuscany, who was 
soon to become one of the founders of the Florentine Accademia del 
Cimento (Academy of Experiment). Ferdinand used this instrument 
for meteorologic purposes and in experiments on the artificial hatching 
of eggs. He also invented an entirely new type of thermoscope (Plate I, 
5) , consisting of a number of blown glass bubbles suspended in alcohol, 
their weights being adjusted so that first one and then another would 
sink as the temperature rose and the density of the alcohol decreased. 

The Accademia del Cimento, during its brief existence from 1657 to 
1667, manufactured many temperature-measuring devices, mainly of 
the alcohol-in-glass expansion type. They were marvels of glass blowing 
(Plate I, 4) and were long used for meteorologic and other purposes in 
different parts of the world. The divisions on the scale were marked 
by minute glass beads of different colors attached to the stem, and the 
scale on the stem was constructed by dividing into a number of equal 
parts the space between the two marks indicating "the most severe 
winter cold" and "the greatest summer heat." Since these two extreme 

PLATE I. Thermometers of the Accademia del Cimento. 


temperatures could not be determined with any precision, no standard 
thermometric system was established by their use. However, this Floren- 
tine scheme for constructing a scale eventually made possible a univer- 
sally comparable measure of temperature. The main problem, it turned 
out, was to find temperatures for determining the fixed marks that could 
be reproduced experimentally with precision. 

The one-fixed-point method of calibration, 1665. Another method of 
calibration affording a universally comparable measure of temperature 
was independently proposed in 1665 by Robert Boyle, Robert Hooke, 
and Christiaan Huygens. This is to mark on the thermometer stem a 
single fixed point, which is to be determined experimentally and is to 
serve as a starting point; and then to place "degree" marks on the stem, 
each of them corresponding to an expansion or contraction of a certain 
fraction say i/iooo, or 1/10,000 of the volume of the thermometric 
substance when at the temperature corresponding to the fixed point. 
For the temperature to be used in establishing the single fixed point, 
Boyle suggested the freezing temperature of oil of aniseed; Hooke, the 
freezing temperature of water; and Huygens, either the freezing or 
the boiling temperature of water. 

The two-fixed-point method of calibration, 1669-1694. The method 
used on Florentine thermometers, in which the space between two 
fixed marks is divided into a number of equal parts, or "degrees," is 
called the two-fixed-point method. In 1669, Honore Fabri, a Jesuit who 
had been a corresponding member of the Accademia del Cimento, 
adopted the temperature of melting snow to determine the lower fixed 
point; but for the upper fixed point he retained the indefinite "greatest 
summer heat." 

Dalence, in 1688, suggested that the temperature for the upper fixed 
point be changed to the melting temperature of butter, thus affording 
greater precision and more nearly comparable readings. He assigned 
the respective values 10 and +10 to his two fixed points, and 
divided the interval between them into 20 equal parts. 

In 1694, the freezing and the boiling temperatures of water were pro- 
posed as the two fixed-point temperatures by Carlo Renaldini, a pro- 
fessor at Padua and a former member of the Accademia del Cimento. 
He divided the interval between these fixed points into 12 equal parts, 
possibly because the number 12 is easily subdivided or because there 
are 12 inches to the foot. 

Eventually it became clear that both the melting temperature of ice 
and the boiling temperature of water are influenced by changes in the 
atmospheric pressure. So it was agreed that these two temperatures when 
the pressure is one standard atmosphere shall be used to establish the 

124 CASE 3 

fixed points; these points are referred to as the ice point and the 
steam point. 

First air thermometer, 1699-7 702. The first air thermometer that was 
not at the same time a barometer was developed by Guillaume Amon- 
tons, a French physicist. In one form of this instrument, the pressure 
of the air is kept constant, and temperatures are measured by observing 
changes in the volume of the air. In another form the one first devel- 
oped by Amontons the volume of the air is kept constant, and tem- 
peratures are measured by observing changes in the pressure of this 
air, instead of in its volume. In other words, air is here the thermometric 
substance, and either its volume or its pressure is the thermometric 

Origin of the Fahrenheit system, 7702-7777. Ole Roemer (R0mer), 
the Danish astronomer, proposed in 1702 that the temperature of a cer- 
tain mixture of ice and salt be made the lower fixed point and assigned 
the value o, and that the steam point be made the upper fixed point 
and assigned the value 60. Thus this was a sexagesimal system. G. D. 
Fahrenheit, who was a celebrated maker of meteorologic instruments, 
visited Roemer in Copenhagen in 1708 and subsequently undertook the 
calibration of thermometers along similar lines. In 1717 he proposed a 
scheme essentially like the one that is today called the "Fahrenheit sys- 
tem," in which the values 32F and 2i2F are assigned to the ice and 
steam points, respectively. 

Fahrenheit was the first to use a cylindrical rather than a spherical 
bulb in thermometers, and contributed in other important ways to the 
art of thermometry by his improved methods of making reliable alcohol- 
in-glass and mercury-in-glass thermometers. Mercury had previously 
been used in barometers and, to some extent, as a thermometric sub- 
stance, but no one before Fahrenheit seems to have thoroughly ap- 
preciated its advantages over other liquids for this purpose. 

Origin of the centigrade system, 77/0-7743. What today is known as 
the "centigrade system," in which the values oC and iooC are as- 
signed to the ice and steam points, is believed to have been first suggested 
as early as 1710 by Elvius, a Swede. It was later proposed, seemingly 
independently, by the eminent Swedish botanist, Linnaeus, in 1740, 
and by Christian of Lyons in 1743. This system is often credited to 
Anders Celsius, a Swedish astronomer, possibly because of a casual 
association suggested by the "C" for centigrade, coupled with the fact 
that Celsius used a centesimal system as early as 1742. However, Celsius' 
system was inverted with respect to the centigrade in that he assigned 
the values 100 and o to the ice and steam points. 

Some recent developments. It eventually became clear chat* the prop- 
erties of different substances are not generally the same functions of 


temperature and, therefore, that thermometers constructed from differ- 
ent substances do not agree exactly with one another at temperatures 
other than the fixed points. So it was desirable that a particular thermo- 
metric substance, together with some particular property of this sub- 
stance, be chosen to serve as the ultimate standard in practical ther- 
mometry. In the nineteenth century, H. V. Regnault showed that the 
constant-volume hydrogen thermometer was highly suitable for this 
purpose; it was adopted as the practical standard and was so used 
until 1927. 

Because of experimental difficulties in the use of any gas thermometer, 
the Seventh General Conference on Weights and Measures, with a 
representation of 31 nations, adopted in 1927 a standard working scale 
designated as the international temperature scale. This scale is defined 
by a series of fixed points, which have been determined by gas-thermom- 
eter measurements, and by the specification of suitable thermometers 
for interpolating between the fixed points and extrapolating to higher 
temperatures. For example, the platinum electrical-resistance thermom- 
eter is used in the range 190 to 66oC, and for higher temperatures 
thermoelectric and optical thermometers are employed. 

Among liquids, mercury is found to agree fairly closely with the gas 
scale, and mercury-in-glass thermometers are still used in cases where 
facility of observation is more important than the highest attainable 
degree of precision. 


The invention of the thermometer provided the means for 
developing not only thermometric measurements but an entirely new 
science that of heat measurements, and the pioneer in the latter devel- 
opment was Joseph Black (1728-1799). Black, as a young man, studied 
medicine, first at the University of Glasgow, and then at the University 
of Edinburgh, where he received the M.D. degree in 1754. It was dur- 
ing these years that he started his researches in chemistry and probably 
also began to form his new ideas about heat. 

In 1756 Black returned to Glasgow as a professor. It was here, during 
the three years between 1759 and 1762, that he made his main discoveries 
in heat. In 1766 he returned to Edinburgh, where he occupied the chair 
of medicine and chemistry until his death. During all these years he 
also engaged extensively in the private practice of medicine. 

Until Black made his discoveries, there was no clear distinction In 
people's minds between the concepts of "quantity of heat" and "degree 

126 CASE 3 

o hotness," or "temperature." The qualitative idea of "heat" as a "some- 
thing" concerned with thermal phenomena had long existed, of course. 
The simple fact that an object close to a fire warms up, which surely 
was known from the time when man discovered fire, must have sug- 
gested that something passes from the fire to the object. But to these 
early people, this something that passes might well have been thought 
to be temperature, or degree of hotness, itself; or, again, it might be a 
separate something, called "heat," this heat and the resulting increase 
in hotness of the object seeming to play the respective roles of cause 
and effect. 

To have clarified these ideas would have been almost impossible as 
long as people had to depend mainly on their thermal sense organs for 
a knowledge of thermal phenomena. The thermal sense organs, as is 
now known, generally afford us judgments that depend not on temper- 
ature alone but on a blend of several thermal properties of a body. For 
instance, if we touch metal and wood in cold weather, the metal will 
"feel" colder than the wood, even though a thermometer applied to 
these objects will show them to be at the same temperature. 

The clarification started only after the invention of the thermometer, 
near the beginning of the seventeenth century. Thus Francis Bacon 
(1620) and, after the middle of the seventeenth century, the members of 
the Florentine Academy, showed evidence of distinguishing between 
temperature and heat. But it was Black who, in the middle of the 
eighteenth century, made the distinction sharp and who, moreover, was 
the first to conceive clearly of heat as a measurable physical quantity, 
distinct from, although related to, the quantity indicated by a thermom- 
eter and called temperature. 

Black never published his great discoveries on heat, although he taught 
them in his academic lectures. These lectures, which also incorporated 
his chemical researches, were published in 1803, after his death, being 
written out by John Robison from Black's notes and those taken by 
some of his students. "Black's heavy duties, ill health, lack of initiative, 
and almost morbid horror of generalization prevented him from going 
further than forming a plan" for a book. 

Robison dedicated the Lectures to James Watt (1736-1819) in a letter, 
printed at the beginning of volume I, of which the following is a part: 

Dear Sin 

By placing your name in the front of this edition of the Lectures of 
our excellent Master, I think that I pay my best respects to his memory, 
and also do a service to the Public. By thus turning the Reader's attention 
to Dr. Black's most illustrious Pupil, I remind him of the important 
services derived from his discoveries: for surely nothing in modern times 


has made such an addition to the power of man as you have done by your 
improvements on the steam engine, which you profess to owe to the 
instructions and information you received from Dr. Black. . . . 

I show the Reader, in your example, that there is no preeminence in 
scientific attainment which he may not hope to reach by rigidly adhering 
to the sober plan of experimental inquiry, so constantly inculcated by 
Dr. Black; and turning a deaf ear to all the fascinating promises of 
splendid theories. The spark, which I thus throw out, may chance to 
light among suitable materials some j dices animce, quibus hcec 
cognoscere curce est minds perhaps unconscious of their own powers. 
Even yours might have lain dormant, had not Dr. Black discovered its 
latent fire. . . . 

Early in his lectures, Black mentions the various theories that had 
been devised to explain the nature of heat what heat "really is." But 
he warns his listeners that one cannot properly understand these theories, 
or how they are applied, until one has become acquainted with the 
effects of heat and with some discoveries that preceded the theories and 
gave occasion to them: 

Our first business must, therefore, necessarily be to study the facts 
belonging to our subject, and to attend to the manner in which heat 
enters various bodies, or is communicated from one to another, together 
with the consequences of its entrance, that is, the effects that it produces 
on bodies. These particulars^ when considered with attention, will lead 
us to some more adequate knowledge and information upon the subject 
which again will enable you to examine and understand the attempts 
that have been made to explain it, and put you in the way to form a 
judgment of their validity. 

The part of the Lectures devoted to the subject of heat covers some 
225 printed pages. Thus the excerpts that appear in the present docu- 
ment represent only a very small fraction of the whole. However, they 
have been selected so as to bring out Black's main discoveries. 

[Excerpts from Volume I of] 

Delivered in the University of Edinburgh 

by the late 


Professor of Chemistry in that University 

Physician to His Majesty for Scotland; Member 

of the Royal Society of Edinburgh, of the 

Royal Academy of Sciences at Paris, 

128 CASE 3 

and the Imperial Academy of 
Sciences at St. Petersburg!! 

Now published from his Manuscripts 


John Robison, LL.D. 

Professor of Natural Philosophy in the University 

of Edinburgh 


Of the Distribution of Heat 

An improvement in our knowledge of heat, which has been attained 
by the use of thermometers, is the more distinct notion we have now 
than formerly of the distribution of heat among different bodies. Even 
without the help of thermometers, we can perceive a tendency of heat to 
diffuse itself from any hotter body to the cooler ones around it, until the 
heat is distributed among them in such a manner that none of them is 
disposed to take any more from the rest. The heat is thus brought into 
a state of equilibrium. 

This equilibrium is somewhat curious. We find that, when all mutual 
action is ended, a thermometer applied to any one of the bodies under- 
goes the same degree of expansion. Therefore the temperature of them all 
is the same. No previous acquaintance with the peculiar relation of each 
body to heat could have assured us of this, and we owe the discovery 
entirely to the thermometer. We must therefore adopt, as one of the most 
general laws of heat, the principle that all bodies communicating freely 
with one another, and exposed to no inequality of external action, acquire 
the same temperature, as indicated by a thermometer. All acquire the 
temperature of the surrounding medium. 

By the use of thermometers we have learned that, if we take a thou- 
sand, or more, different kinds of matter such as metals, stones, salts, 
woods, cork, feathers, wool, water and a variety of other fluids although 
they be all at first of different temperatures, and if we put them together 
in a room without a fire, and into which the sun does not shine, the heat 
will be communicated from the hotter of these bodies to the colder, dur- 
ing some hours perhaps, or the course of a day, at the end of which time, 
if we apply a thermometer to them all in succession, it will give precisely 
the same reading. The heat, therefore, distributes itself upon this occasion 
until none of these bodies has a greater demand or attraction for heat 
than every other of them has; in consequence, when we apply a thermom- 
eter to them all in succession, after the first to which it is applied has 
reduced the instrument to its own temperature, none of the rest is dis- 
posed to increase or diminish the quantity of heat which that first one 
left in it. This is what has been commonly called an "equal heat," or "the 


equality of heat among different bodies"; I call it the equilibrium of heat. 

The nature of this equilibrium was not well understood until I pointed 
out a method of investigating it. Dr. Boerhaave imagined that when it 
obtains, there is an equal quantity of heat in every equal volume of space, 
however filled up with different bodies; and Professor Musschenbroeck, 
in his Physica, expressed his opinion to the same purpose: "Est enim 
ignis aequaliter per ornnia, non admodum magna, distributus, ita ut in 
pede cubico auri et aeris et plumarum, par ignis sit quantitas." ["For 
the heat is distributed through all (the bodies), not in proportion to their 
(weight), so that in a cubic foot of gold and of air and of feathers, there 
will be an equal quantity of heat.] The reason they give for this opinion 
is that, to whichever of those bodies the thermometer be applied, it gives 
the same reading. 

But this is taking a very hasty view of the subject. It is confounding 
the quantity of heat in different bodies with its intensity [temperature], 
though it is plain that these are two different things, and should always 
be distinguished, when we are thinking of the distribution of heat. . . . 

Hermann Boerhaave (1668-1738) was a great teacher of medicine at 
the University of Leiden who performed a useful service by collecting 
and classifying the scientific knowledge of his period and publishing 
it in textbooks on medicine (1708) and on chemistry (1732). Pieter van 
Musschenbroeck (1692-1761) went to Leiden in 1740 as professor o 
philosophy; he also wrote extensively on physical science. 

As Black says, Boerhaave and Musschenbroeck thought that, if a 
number of different objects were placed in, say, a room and allowed 
to remain there until all had acquired the same temperature, as indicated 
by a thermometer, then this meant that heat was also distributed uni- 
formly throughout the room and its contents that every cubic inch 
of space in the room, whether it be occupied by wood, metal, air, or 
anything else, contained the same quantity of heat. On the contrary, 
asserts Black, when the various objects have come to the same tempera- 
ture, there exists, not an equal distribution of heat throughout the 
room, but what he calls an "equilibrium of heat," meaning that there 
is no longer any flow of heat among the objects. Notice that temperatures 
are observed with a thermometer, whereas Black's notion that a some- 
thing called heat passes from bodies of higher temperature to those of 
lower temperature is of the character of a hypothesis. 

In the section that follows, on "Capacities for Heat," Black investi- 
gates the question of the quantities of heat needed to increase the tem- 
peratures of different bodies by the same amount. He says that it was 
formerly supposed that these required quantities of heat were directly 
proportional to the "quantities of matter" in the bodies; or, since the 
"quantities of matter" in different bodies can be compared by compar- 

130 CASE 3 

ing the weights o the bodies when they are in the same locality, that 
the required quantities of heat were supposed to be directly proportional 
to the weights of the bodies. If this hypothesis were correct, the quantity 
of heat needed to warm i Ib of mercury through, say, one Fahrenheit 
degree would be the same as that needed for i Ib of water; and to 
produce the same temperature change in 2 Ib of mercury would require 
twice as much heat as for i Ib of water, or of mercury, or of any other 

Black subsequently shows that this hypothesis is not generally valid. 
The argument that he uses will perhaps be made easier to follow if we 
first restate the hypothesis in algebraic language, which he did not use. 
Let the symbol HI signify the quantity of heat .that must be added to 
a body of weight w in order to increase its temperature by an amount 
A*. (The Greek capital letter delta is used to express a difference be- 
tween two values of the quantity symbolized by the letter that follows 
it in this case t for temperature; for instance, if water is warmed 
from its freezing temperature, 32F, to its boiling temperature, 2i2F, 
then A/ is equal to 2i2F 32F, or i8oF.) Similarly, let H 2 signify 
the quantity of heat needed to produce the same temperature change 
At in another body of weight w^ By using these symbols, the foregoing 
hypothesis may now be expressed in the form 

_ 1 _. _ L (F r the same temperature / \ 


We shall see (p. 23) that Black finds it useful to restate this faulty 
hypothesis in another, alternative way, namely, that the quantities of 
heat needed to produce the same temperature change in bodies of the 
same volume are proportional to the densities of the bodies. To convert 
our Eq. (i) to this alternative form, recall, first, that the weight-density 
D of any object is, by definition, the weight w of the object divided by 
its volume F; that is, D = w/V. Now, multiply both members of this 
defining equation by F, thus changing it to the form w = DV. Finally, 
replace w in Eq. (i) by DiV, and u/z by D 2 F, thus giving 

Hi DiV Di (For the same temperature 

\j sss ' T _ == change A/ in bodies of the (2) 

/12 DzV Dz same volume) 

For instance, the density of mercury is about 14 times that of water. 
Therefore, according to Eq. (2), the quantity of heat needed to warm 
mercury through, say, one Fahrenheit degree should be 14 times that 
needed for equal warming of the same volume of water. As we shall 
see, Black finds that this prediction is far from being in accord with 


In our subsequent notes, we shall find it convenient to refer to the 
hypothesis expressed by either Eq. (i) or Eq. (2) as the "weight 

Capacities for Heat 

It was formerly a common supposition that the quantities of heat re- 
quired to increase the temperatures of different bodies by the same num- 
ber of degrees were directly proportional to the quantities of matter in 
them [and thus to their weights] ; and therefore, when the bodies were 
of equal volumes, that the quantities of heat were proportional to their 
densities [and thus to their weights per unit volume]. But very soon after 
I began to think on this subject (anno 1760), I perceived that this opinion 
was a mistake, and that the quantities of heat which different kinds of 
matter must receive to raise their temperatures by an equal number of 
degrees are not in proportion to the quantity of matter in each, but in 
proportions widely different from this, and for which no general principle 
or reason could yet be assigned. 

This opinion was first suggested to me by an experiment described 
by Dr. Boerhaave in his Elementa Chemice [1732]. After relating an 
experiment on the mixing of hot and cold water which Fahrenheit made 
at his desire, Boerhaave also tells us that Fahrenheit agitated together 
quicksilver [mercury] and water of initially different temperatures. From 
the Doctor's account, it is quite plain that the quicksilver, though it has 
more than 13 times the density of water, had less effect in heating or 
cooling the water with which it was mixed than would have been pro- 
duced by an equal volume of water. He says expressly that the quick- 
silver, whether it was applied hot to cold water, or cold to hot water, 
never produced more effect in heating or cooling an equal volume of the 
water than would have been produced by water of the same initial tem- 
perature as the quicksilver, and only two-thirds of its volume. He adds 
that is was necessary to mix three volumes of quicksilver with two of 
water in order to produce the same middle temperature that is produced 
by mixing equal volumes of hot and cold water. 

To make this plainer by an example in numbers, let us suppose the 
water to be at iooF and that an equal volume of warm quicksilver at 
I50F is suddenly mixed and agitated with it. We know that the tempera- 
ture midway between 100 and i5oF is i25F, and we know that this 
middle temperature would be produced by mixing cold water at iooF 
with an equal volume of warm water at 150 F, the temperature of the 
warm water being lowered by 25 degrees while that of the cold is raised 
just as much. But when warm quicksilver is used in place of warm water, 
the temperature of the mixture turns out to be only i20F, instead of 
i25F. The quicksilver, therefore, has cooled through 30 degrees, while 
the water has become warmer by 20 degrees only; and yet the quantity 
of heat which the water has gained is the very same as that which the 
quicksilver has lost. This shows that the same quantity of heat has more 

132 CASE 3 

effect in warming quicksilver than in warming an equal volume of 
water, and therefore that a smaller quantity of it is sufficient for increas- 
ing the temperature of quicksilver by the same number of degrees. 

This is true, whatever way we vary the experiment. Thus, if the water 
is the warmer mass, and the equal volume of quicksilver the cooler one, 
by the aforementioned difference, the temperence of the mixture will be 
130?; the water, in this case, cools through 20 degrees, while the heat 
it has given to the quicksilver makes this warmer by 30 degrees. And 
lastly, if we take 3 volumes of quicksilver to 2 of water, it does not matter 
which of them is the hotter; the temperature of the mixture always will 
be the middle temperature between the two. Here it is manifest that the 
quantity of heat which makes 2 volumes of water warmer by, say, 25 
degrees is sufficient to make 3 volumes of quicksilver warmer by the 
same number of degrees. Quicksilver, therefore, has less capacity for 
heat (if I may be allowed to use this expression) than has water; a smaller 
quantity of heat is needed to raise its temperature by the same number 
of degrees. 

G. D. Fahrenheit (1668-1736) seemingly never published an account 
of the mixing experiments which Boerhaave attributed to him. Boer- 
haave, in his Elementa Che-mice, said that Fahrenheit first mixed equal 
volumes of cold and hot water, and found the temperature of the result- 
ing mixture to be midway between the two initial temperatures. For in- 
stance, when the initial temperatures were 40 and 8oF, the tempera- 
ture of the mixture turned out to 60 F. 

Let us see what light is thrown on this experimental result of Fahren- 
heit's by the weight hypothesis. Fahrenheit found that when equal 
volumes of the same liquid are mixed, the rise in temperature At of the 
cold liquid is numerically equal to the drop in temperature A/ of the 
warm liquid. Moreover, since the two liquids are the same, their 
densities Di and D 2 are tne same. So our Eq. (2) becomes for this case, 

or HI = H 2 . According to this result, the quantity of heat HI gained 
by the cold liquid is equal to quantity H 2 lost by the warm liquid dur- 
ing the mixing. The same conclusion was reached in similar experi- 
ments on the mixing of unequal volumes of cold and hot water, made 
at about this time (ca. 1723) by Brook Taylor; he found that the tem- 
perature of the mixture could be successfully predicted on the assump- 
tion that the heat gained by the cold liquid is equal to that lost by the 
warm liquid. 

This assumption was extended by Black to explain the effects of mix- 
ing, not only the same liquids, but any volumes of different liquids; 


for he says (p. 23), "and yet the quantity of heat which the water has 
gained is the very same as that which the quicksilver has lost." Actually, 
two assumptions are involved in his and all subsequent explanations 
of mixing experiments, namely, (i) that heat is neither created nor 
destroyed during the mixing and (ii) that account must be taken of 
any heat lost to or gained from the air or other bodies in contact with 
the mixture. The first of these assumptions is called the "principle of 
conservation of heat." This principle seemed to be plausible for, as we 
shall eventually see, it was rather generally believed in Black's day that 
heat was a material substance, having many of the properties of ordinary 
matter; and since the time of the Greeks the idea had persisted that 
matter was uncreatable and indestructible, However, it is important to 
note that the possibility of using this principle in calculations of mix- 
ture temperatures first became apparent through consideration of the 
weight hypothesis [Eq. (i) or (2)]. Yet, as Black has shown in the 
preceding pages, the weight hypothesis predicts correct mixture tem- 
peratures only when the same substances are mixed, whereas the prin- 
ciple of conservation of heat is assumed by him to apply in all mixing 
experiments. The weight hypothesis is less generally valid than the 
new principle that it has suggested. 

As Black says, the results obtained by Fahrenheit in mixing water 
and mercury indicate that the quantities of heat needed to produce the 
same temperature change in different substances depends, not merely 
on their weight, but also on their different capacities for heat, the mer- 
cury evidently having a smaller capacity for heat than the water. 

The inference that Dr. Boerhaave drew from Fahrenheit's experiment 
is very surprising. Observing that heat is not distributed among different 
bodies in proportion to the quantity of matter in each [and therefore the 
weight of each], he concluded that it is distributed in proportion to the 
volume of each body a conclusion contradicted by this very experi- 
ment. Yet Musschenbroeck has followed him in this opinion. 

Boerhaave saw for himself that the weight hypothesis our Eq. (i) 
did not correctly predict the mixture temperature when two different 
substances, such as mercury and water, are mixed. So he advanced an- 
other hypothesis, namely, that the quantities of heat needed to produce 
the same temperature change in any two bodies were directly propor- 
tional to the volumes of the bodies, or, in algebraic language, that 

^ 1 * (^ or ^ e &ame tem P erature (S\ 

W 2 ~V^* change A/) 

This "very surprising" inference, which we shall call the "volume 
hypothesis," is seen to have the same limited validity as the weight 

134 CASE 3 

hypothesis; that is, It predicts results in accord with experiment only 
when two liquids of the same kind are mixed, for instance, water and 
water, or mercury and mercury. But, for equal volumes of different 
liquids, the volume hypothesis predicts that equal quantities of heat 
should be needed to produce the same temperature changes. Yet Fahren- 
heit's experiments indicated that equal quantities of heat produced the 
same temperature changes, not in equal volumes of water and mercury, 
but in two volumes of water and three of mercury. 

As soon as I understood this experiment [of Fahrenheit's] in the 
manner I have now explained it, I found a remarkable agreement be- 
tween it and some experiments described by Dr. Martine, in his "Essay 
on the heating and cooling of bodies" [1740]. His experiments appeared 
at first very surprising and unaccountable, but, being compared with 
this one, may be explained by the same principle. Dr. Martine placed 
before a good fire, and at equal distances from it, some water and an 
equal volume of quicksilver, each of them contained in equal and similar 
glass vessels, and each having a delicate thermometer immersed in it. 
He then carefully observed the celerity with which each of these liquids 
was heated by the fire, as indicated by the thermometers. He found, by 
repeated trials, that the quicksilver was warmed by the fire almost twice 
as fast as the water; and after each trial, having heated these two liquids 
to the same temperature, he placed them in a stream of cold air and 
found that the quicksilver always cooled much faster than the water. 
Before these experiments were made, it was supposed [on the basis of 
the weight hypothesis] that the time needed for the quicksilver to heat 
or cool would be longer than for an equal volume of water, in the pro- 
portion of 13 or 14 to one. 

But, from the view I have given of Fahrenheit's experiment with quick- 
silver and water, the foregoing experiment of Dr. Martine's is easily ex- 
plained. We need only to suppose that the fire communicated equal 
quantities of heat to both liquids, but that, as less of it was required for 
warming the quicksilver than for warming the water, the quicksilver 
necessarily was warmed the faster of the two. And when both, being 
raised to the same temperature, were exposed to the cold air, the air at 
first received heat from them equally fast, but the quicksilver, by losing 
the same quantity of heat as the water, became cold much faster than 
the water. These experiments of Dr. Martine's, in thus agreeing so well 
with Fahrenheit's, plainly show that quicksilver, notwithstanding its 
larger density, requires less heat to produce a given temperature rise 
than is necessary for an equal volume of water. The quicksilver, there- 
fore, may be said to have less capacity for the matter of heat. And we are 
thus taught that, in cases in which we may have occasion to investigate 
the capacities of different bodies for heat, we can learn them only by 
making experiments. Some have accordingly been made, both by myself 
and others. 


George Martine (1702-1741), a physician who served for a time in 
the British Army in America, was a skilful experimenter who published 
a number of scientific papers in a volume entitled Essays, Medical and 
Philosophical (London, 1740). In the experiment just described, he 
made use of what has since come to be called "the method of constant 
heat supply." The substance to be heated is exposed to a fire or other 
source of heat that is sufficiently steady to warrant the assumption that 
heat is supplied at a constant rate; in other words, that the quantity of 
heat H absorbed by the substance is directly proportional to the time T 
during which the substance is exposed to the source. One is reminded 
here of the inverse, ancient practice of measuring the passage of time 
by observing the rate at which a candle burns away. 

If the weight hypothesis our Eq. (2) were correct, mercury, 
whose density is 13.6 times that of water, should rise in temperature 
only 1/13.6 as fast as the same volume of water, when both are exposed 
to the same fire. But Martine found, "contrary to the common opinion," 
that the mercury actually warmed about twice as fast as the water. 

Nor could Martine's result be predicated by Boerhaave's volume 
hypothesis our Eq. (3). According to it, equal volumes of mercury 
and water should warm through the same temperature interval in the 
same time. 

Martine made similar experiments with other pairs of unlike liquids, 
noting the time needed for them to warm, and also to cool after being 
warmed, and in no case was the result in accord with either the weight 
or the volume hypothesis. In his essay describing these experiments, Mar- 
tine said that, contrary to all our fine theories, quicksilver, the most dense 
ordinary fluid in the world, excepting only melted gold, is, however, 
the most ticklish next to air; it heats and cools sooner than water, oil, 
or even rectified spirits of wine itself; and he was moved to say that he 
knew "no stronger instance than this of the weakness, or, if I may 
venture to say so, of the presumptuousness of the human understand- 
ing, in pronouncing too hastily concerning the nature of things from 
some general preconceived theories." 

Although Black says (p. 134). that he carried out experiments to deter- 
mine what he called the "capacity for heat" of various substances, he 
does not describe them anywhere in his lectures. However, Robison 
states in his "Notes and Observations by the Editor," at the end of 
volume I, that Black made many such experiments prior to 1765 and 
was assisted in them by William Irvine (1743-1787), who studied under 
him and later became Lecturer in Chemistry at Glasgow. Robison 
says that these experiments were carried out by the method of mixtures, 
which both Fahrenheit and Brook Taylor (p. 132) had used to a limited 

136 CASE 3 

extent, 'but which Black developed so as to be able to measure "capaci- 
ties for heat." 

Later, Martine's method of constant heat supply was also used for 
this purpose. By putting different weights w of a particular substance 
in a vessel and exposing each of them to a steady fire for varying periods 
of time, Black found that the time of heating, and therefore the quantity 
of heat H added, is directly proportional both to the weight w of 
substance and to the rise in temperature A/; that is, H & tvAt for a 
given substance. Now any statement of proportionality, such as this, 
may be converted into an equation by introducing a proportionality 
factor. Denoting this factor in the present case by the symbol s and 
inserting it in the foregoing expression, we obtain 

H = swLt. (4) 

Black's great achievement here was to show that the value of this 
factor s is different for every different substance. He and Irvine referred 
to the factor variously as "affinity for heat," "faculty for receiving heat" 
and "appetite for heat," but finally settled on the term "capacity for 
heat." Later experimenters, such as Adair Crawford, the author of a 
well-known book entitled Experiments and Observations on Animal 
Heat (1779)? and J. C. Wilcke (1781), a Swedish physicist, used various 
other terms; but Wilcke finally adopted specific heat for the factor s, 
and this is the term most widely used today. 

Nothing has yet been said about units for measuring heat H and 
specific heat s. Richard Kirwan, a contemporary of Black's, seemingly 
was the first to suggest that the specific heats of various substances be 
measured with respect to that of water taken as a standard, and this is 
the practice still followed today. However, the early methods of ex- 
pressing specific heats were varied and somewhat complicated, and thus 
we will find it better to introduce modern units at this point. 

The unit for quantity of heat H called the British thermal unit 
(symbol, Btu) is defined as the quantity of heat that enters or leaves 
i Ib of water when it undergoes a temperature change of one Fahren- 
heit degree. In other words, when Eq. (4) is applied to water, H is I 
Btu when w is i Ib and A2 is i Fahrenheit degree; thus 

iBtu*=^ water XilbXi F, 

^ water = i Btu/lb R 

Notice that the specific heat s of any substance is, by definition, the 
quantity of heat that enters or leaves i Ib of the substance when its 
temperature changes by one Fahrenheit degree. For water, the specific 


heat is i Btu/lb F, by definition. For other substances, as Black points 
out (p. 134)5 the specific heats must be found by experiment. For in- 
stance, experiment shows that the specific heat of mercury is 0.033 
Btu/ib F. 

Li quej action 

Our experience of freezing of liquids when exposed to more or less 
powerful degrees of cold is almost universal. The exceptions are very 
few. The strongest spirit of wine [alcohol] and a few subtle and volatile 
oils are the only substances that have not yet been solidified by any degree 
of cold hitherto known. As these, however, are so few in number, it ap- 
pears unreasonable to believe them to be so different in nature and con- 
stitution from all other bodies that liquidity is in them an essential 
quality, of which they cannot be deprived by any diminution of their 
neat. We have no certain knowledge of what is the lowest possible tem- 
perature, but, on the contrary, shall have reason hereafter to be persuaded 
that the most violent cold which has yet been observed is very far short 
of the most extreme degree. So it is reasonable to suppose that these few 
substances differ from others only in having a much greater disposition 
to liquidity, so that we have never yet known a degree of cold sufficient 
for solidifying them; but that they would undoubtedly freeze, like other 
liquids, were they exposed to a sufficiently low temperature. 

Quicksilver was, not long since, one of this small number of substances, 
which, having never been seen in any other than a liquid state, was con- 
sidered as naturally and essentially liquid, and incapable of being reduced 
to a solid form, until experiments were made with it, first in different 
parts of the Russian Empire, since the year 1760, and verified afterwards 
in other places. By these experiments, every person must be convinced 
that quicksilver is a metal that can become solid and malleable like the 
rest, but that it freezes at a lower temperature [now known to be about 
38F] than has ever been observed over the greater part of the sur- 
face of this earth. In the same manner may we consider all other liquids 
as solids melted by heat. 

Some philosophers, however, have offered many objections to this 
general proposition concerning the nature of liquids. They thought It 
necessary to suppose that water is an exception. They could not be per- 
suaded that its liquidity is the effect of heat, but supposed this quality 
to be an essential one of the water, depending on the spherical form and 
polished surface of its particles, and that the freezing of it depended on 
the introduction of some extraneous, subtle matter. This opinion is de- 
fended by Professor Musschenbroeck, in his Physica, and he has collected 
all the reasons and arguments which have been devised for supporting 
such an opinion. 

But when we consider these reasons and arguments with due attention, 
we find that none of them are valid. Many of them are alleged facts, 
adduced to prove that water sometimes freezes under circumstances 

138 CASE 3 

such that Mr. Musschenbroeck did not comprehend how it could have 
been cooled to the temperature reckoned necessary for its solidification; 
and he therefore concludes that the freezing of it must have been due to 
some cause other than the diminution of its temperature to the proper 

But had he applied a good thermometer to the water, he would have 
found that it was actually cooled to the usual temperature [32?] in 
every case in which it froze. For the truth of this we may depend on the 
testimony of Dr. Martine, who, with the assistance of his friends, had 
experiments made in many distant parts of the world and at different 
times, with thermometers on which he could entirely rely. There is no 
doubt that many mistakes have been committed by using bad thermom- 
eters, or by the want of skill to use them properly., But the truth is 
that, in the facts adduced by Musschenbroeck, no thermometer whatever 
was applied to the water itself, but only vague reasoning was employed 
to make it appear probable that it was not cooled to the proper tempera- 
ture. We may, therefore, pass over the greater number of his reasons, 
and take some notice of a few of his facts that are surprising in them- 
selves, that could not be explained by any principles then known, and 
that, besides, are so stated by him as to make them appear uncommonly 

In several pages that we are omitting, Black discusses various phe- 
nomena cited by Musschenbroeck for instance, the fact that water 
expands when it freezes and shows that the latter was mistaken in 
thinking that they supported his views. 

Thus many of Professor Musschenbroeck's reasons for his opinion on 
the congelation of water are quite inconclusive, none of them giving any 
satisfactory proof that the liquidity of water is an essential quality or 
that any new matter is introduced when it is frozen. The propensity of 
many people to imagine water as naturally and essentially liquid is a 
prejudice contracted from the habit of seeing it much oftener in this state 
than in the solid state. . . . 

In considering the effect of heat in producing liquefaction, we should 
first remark that innumerable experiments made with thermometers 
show that the change of a particular substance from solid to liquid occurs 
only when the temperature is increased to a certain value. Above this 
temperature the substance is a liquid. If the liquid is cooled back down 
to this temperature, it becomes solid, and it remains solid at all lower 
temperatures. This at least may be stated as the general fact. 

There are, however, many substances [now called amorphous sub- 
stances} in which the transition is not so sudden. These, within a certain 
range of temperatures, are reduced to an intermediate state one of 
softness and pass through all the degrees of it while heat is being added 
to change them from solid to liquid. We have examples of this in bees- 
wax, resin, tallow, glass, and many other substances. But even in these, 


every degree of softness depends on a corresponding temperature, which 
has the power to produce it; and in most of these bodies there is also a 
remarkable step from the greatest degree of softness to perfect liquidity, 
which always depends on a certain temperature necessary to the complete 
liquefaction of that particular body. 

Thus, in general, each different kind of matter must be heated to a 
particular temperature to render it liquid, and below this temperature it 
is either solid or has some degree of solidity. This temperature is there- 
fore called the FREEZING or the MELTING POINT of the substance. It is 
called the freezing point of such substances as exist commonly in the 
liquid state, and the melting point of those that are solid under ordinary 
circumstances. When we compare different kinds of matter, there is all 
the variety that can be imagined between those that require for their 
fusion the highest temperatures and those for which the freezing point 
is so low that they always appear, in ordinary circumstances, in the 
liquid form. . . . 

I must now add that the foregoing general account of liquefaction as 
an effect of heat is not complete and satisfactory, if this effect is inter- 
preted in terms of certain common opinions that have been entertained 
about it opinions that are inconsistent with many remarkable phe- 
nomena. As these phenomena show, when attentively considered, lique- 
faction is produced by heat in a very different manner from that which 
has commonly been imagined yet in a manner which, when under- 
stood, enables us to explain many particulars relating to heat or cold that 
formerly appeared to be quite perplexing and unaccountable. 

Melting had been universally considered as produced by the addition 
of a very small quantity of heat to a solid body, once it had been warmed 
up to its melting point; and the return of the liquid to the solid state, as 
depending on a very small diminution of the quantity of its heat, after 
it had cooled to the same degree. It was believed that this small addition 
of heat during melting was needed to produce a small rise in temperature, 
as indicated by a thermometer placed in the resulting liquid; and that, 
when the melted body was again made to solidify, it suffered no greater 
loss of heat than that corresponding to a drop in temperature of the re- 
sulting solid, indicated also by the application to it of the same instrument. 

This was the universal opinion on the subject, so far as I know, when 
I began to read my lectures in the University of Glasgow in the year 
1757. But I soon found reason to object to it, as inconsistent with many 
remarkable facts, when attentively considered; and I endeavored to show 
that these facts are convincing proofs that liquefaction is produced by 
heat in a very different manner. 

The opinion I formed from attentive observation of the facts and phe- 
nomena is as follows. When ice or any other solid susbtance is melted, I 
am of the opinion that it receives a much larger quantity of heat than 
what is perceptible in it immediately afterwards by the thermometer. A 
large quantity of heat enters into it, on this occasion, without making 

140 CASE 3 

it apparently warmer, when tried by that instrument. This heat must be 
added in order to give it the form of a liquid; and I affirm that this large 
addition of heat is the principal and most immediate cause of the lique- 
faction induced. 

On the other hand, when we freeze a liquid, a very large quantity of 
heat comes our of it, while it is assuming a solid form, the loss of which 
heat is not to be perceived by the common manner of using the ther- 
mometer. The apparent temperature of the body, as measured by that 
instrument, is not diminished, or not in proportion to the loss of heat 
which the body actually suffers on this occasion; and it appears, from a 
number of facts, that the state of solidity cannot be induced without the 
abstraction of this large quantity of heat. And this confirms the opinion 
that this quantity of heat, absorbed, and, as it were, concealed in the 
composition of liquids, is the most necessary and immediate cause of 
their liquidity. . . . 

If we attend to the manner in which ice and snow melt when exposed 
to the air of a warm room, or when a thaw succeeds to frost, we can 
easily perceive that, however cold they might be at first, they soon warm 
up to their melting point and begin to melt at their surfaces. And if the 
common opinion had been well founded if the complete change of 
them into water required only the further addition of a very small quan- 
tity of heat the mass, though of a considerable size, ought all to be 
melted within a very few minutes or seconds by the heat incessantly 
communicated from the surrounding air. Were this really the case, the 
consequences of it would be dreadful in many cases; for, even as things 
are at present, the melting of large amounts of snow and ice occasions 
violent torrents and great inundations in the cold countries or in the 
rivers that come from them. But, were the ice and snow to melt suddenly, 
as they would if the former opinion of the action of heat in melting them 
were well founded, the torrents and inundations would be incomparably 
more irresistible and dreadful. They would tear up and sweep away 
everything, and this so suddenly that mankind would have great diffi- 
culty in escaping from their ravages. This sudden liquefaction does not 
actually happen. The masses of ice or snow require a long time to melt, 
especially if they be of a large size, such as are the collections of ice and 
wreaths of snow formed in some places during the winter; these, after 
they begin to melt, often require many weeks of warm weather before 
they are totally changed into water ... In the same manner does snow 
continue on many mountains during the whole summer, in a melting 
state, but melting so slowly that the whole of that season is not a sufficient 
time for its complete liquefaction. . . . 

If any person entertain doubts of the entrance and absorption of heat 
in the melting ice, he needs only to touch it; he will instantly feel that 
it rapidly draws heat from his warm hand. He may also examine the 
bodies that surround or are in contact with it, all of which he will find 
deprived by it of a large part of their heat; or if he suspend ice by a 


thread in a warm room, he may perceive with his hand, or by a ther- 
mometer, a stream of cold air descending constantly from the ice; for the 
air in contact is deprived of a part of its heat, and thereby contracts and 
is made denser than the warmer air of the rest of the room; it therefore 
falls, and its place round the ice is immediately taken by some of the 
warmer air; but this, in its turn, is soon deprived of some heat, and so 
descends in like manner; and thus there is a constant flow of warm air 
from around to the sides of the ice, and a descent of the same after cool- 
ing, during which operation the ice must necessarily receive a large 
quantity of heat. 

It is evident, therefore, that the melting ice receives heat very fast, but 
the only effect of this heat is to change it into water, which is not in the 
least sensibly warmer than the ice was before. A thermometer applied 
to the drops of water, immediately as they come from the melting ice, 
will indicate the same temperature [32F] as when it is applied to the 
ice itself, or, if there is any difference, it is too small to deserve notice. A 
large quantity, therefore, of the heat which enters into the melting ice 
produces no effect other than to give it liquidity, without augmenting its 
sensible heat; it appears to be absorbed and concealed within the water, 
so as not to produce any effect discoverable by the application of a 

In order to understand better this absorption of heat by the melting ice, 
and concealment of it in the water, I made the following experiments 

I chose two thin globular glasses, 4 inches in diameter, and very nearly 
of the same weight. I poured 5 ounces [apothecaries' weight, equivalent 
to 5.5 oz avoirdupois] of pure water into one of them, and then set it 
in a mixture of snow and salt until the water was frozen into a small 
mass of ice. It was then carried into a large empty hall, in which the air 
was not disturbed or varied in temperature during the progress of the 
experiment. The glass was supported, as it were, in mid-air, by being 
set on a ring of strong wire, which had a 5-inch tail issuing from the side 
of it, the end of which was fixed in the most projecting part of a reading 
desk or pulpit. 

I now set up the other globular glass precisely in the same way, and 
at the distance of 18 inches to one side, and into this I poured 5 ounces 
of water, previously cooled almost to the freezing point actually to 
33 F. Suspended in it was a very delicate thermometer, with its bulb in 
the center of the water, and its stem so placed that I could read it without 
touching the thermometer. I then began to observe the ascent of this ther- 
mometer, at suitable intervals, in order to learn with what celerity the 
water received heat; I stirred the water gently with the end of a feather 
about a minute before each observation. The temperature of the air, 
examined at a little distance from the glasses, was 47R 

The thermometer assumed the temperature of the water in less than 
half a minute, after which, the rise of it was observed every 5 or 10 
minutes, during half an hour. At the end of that time, the water was 7 

142 CASE 3 

degrees warmer than at first; that is, its temperature had risen to 40 F. 

The glass containing the ice was, when first taken out of the freezing 
mixture, 4 or 5 degrees colder than melting snow, which I learned by 
applying the bulb of the thermometer to the bottom of it; but after some 
minutes, it had gained from the air enough heat to warm it those 4 or 5 
degrees, and the ice was just beginning to melt. After an additional ioJ/2 
hours, only a very small and spongy mass of the ice remained unmelted, it 
being in the center of the upper surface of the water, but this also was 
totally melted in a few minutes more. Introducing the bulb of the ther- 
mometer into the water, near the sides of the glass, I found that the 
water there had warmed to 40 F. . . . 

It appears that the ice-glass had to receive heat from the air of the room 
during 21 half-hours in order to melt the ice and then warm the result- 
ing water to 40 F. During all this time it was receiving heat with the 
same celerity (very nearly) as had the water-glass during the single half- 
hour in the first part of the experiment . . . Therefore, the quantity of 
heat received by the ice-glass during the 21 half-hours was 21 times the 
quantity received by the water-glass during the single half-hour. It was, 
therefore, a quantity of heat, which, had it been added to liquid water, 
would have made it warmer by (40 33) X 2r > or 7 X 21, or 147 de- 
grees. No part of this heat, however, appeared in the ice-water, except 
that which produced the temperature rise of 8 degrees; the remaining 
part, corresponding to 139 or 140 degrees, had been absorbed by the 
melting ice and was concealed in the water into which it was 
changed. . . . 

In this experiment, Black has used Marline's method of constant heat 
supply (p. 134) , the constant source of heat here being the air of the 
room. Let us repeat Black's calculation in terms of modern units and 
using Eq. (4), p. 136, To simplify the calculation, we will assume that 
the contents of each glass weighed i Ib avoirdupois, instead of 5 oz 
apothecaries' weight. This will not change the final result, but means 
merely that the room temperature would have to be considerably 
higher than was Black's in order for the temperature changes and time- 
intervals to be the same as he observed. 

In the water-glass, i Ib of water underwent a temperature rise A* of 
7 Fahrenheit degrees in i half -hour. Since the specific heat of water is 
i Btu/lb F, the quantity of heat H that passed from the air into this 
water in i half -hour was 

H = swte = i X i Ib X 7F = 7 Btu. 


For the ice-glass, the quantity of heat absorbed by its contents in 21 
half-hours was 21 Jf, or 21 X 7 Btu, or 147 Btu. Some of this heat served 
to warm the i Ib of melted ice through 8 Fahrenheit degrees, this part 


evidently amounting to 8 Btu. The remainder, or 139 Btu, "had been 
absorbed by the melting ice and was concealed in the water into which 
it was changed." 

This discovery of Black's suggested that it would be useful to define 
a new physical quantity, which has come to be called the heat of fusion 
of a substance, symbol h t . It is defined as the quantity of heat required 
to melt unit weight of a solid substance without any change of tem- 
perature taking place. Thus Black's present experiment yields a value 
of 139 Btu/lb for the heat of fusion of ice. The modern value is 144 

In the next experiment, Black uses the method of mixtures to obtain 
data for another determination of the heat of fusion of ice. 

Another obvious method of melting ice occurred to me, in which it 
would be still easier to perceive the absorption and concealment of heat, 
and this was by the action of warm water. . . . 

If equal weights of hot and cold water are mixed together, the tem- 
perature of the mixture is halfway between that of the hot and that of 
the cold. No part of the heat disappears on this occasion, so far as we 
can perceive, only the intensity of it [the temperature] being diminished 
by the heat's being diffused through a larger quantity of matter. It was 
obvious, therefore, that if a quantity of heat is absorbed and disappears 
in the melting of ice, this would easily be perceived when the ice is 
melted by mixing it with warm water. 

To make this experiment, I first froze some water in the neck of a 
broken retort, in order to have a mass of ice of an oblong form. At the 
same time I heated some water, nearly equal in weight to the ice, in a 
very thin globular glass, the mouth of which was sufficiently wide to ad- 
mit the piece of ice. The water was heated by a small spirit-of-wine lamp; 
it was also often stirred with the end of a feather, and had a thermometer 
hung in it. 

While the water was heating, the mass of ice was taken out of the 
mould and was exposed to the air until it was beginning to melt over the 
whole of its surface. I then put a woolen glove on my left hand and, 
taking hold of the ice, wiped it quite dry with a linen towel, laid it in the 
pan of a balance on a piece of flannel, and hastily counterpoised it with 
sand in the opposite pan, so that I might examine its weight afterwards. I 
immediately plunged it into the hot water, and at the same time extin- 
guished the lamp. The lamp being small, the temperature of the water 
had been increasing very slowly, and had almost ceased to increase; 
immediately before I put the ice into it, this temperature was found to be 
just 190 F. The ice was all melted in a few seconds and produced a 
mixture, the temperature of which was 53 F. , . . 

The melting of the ice was effected, not only by the heat from the hot 
water, but also by that from the glass. From other experiments I learned 
that 1 6 parts [by weight] of hot glass have no more power in heating 

144 CASE 3 

cold bodies than do 8 parts of equally hot water; we may therefore sub- 
stitute, in place of the 16 half-drams of warm glass, 8 half-drams of 
warm water, which, added to the 135 half-drams of warm water, make 
up 143 half-drams. . . . 

Since the calculations to which Black now proceeds are carried out 
in a somewhat complicated fashion, we are replacing them here by the 
simpler method in common use today. Moreover, we are substituting 
more convenient values for the weights of the materials and are ex- 
pressing them in pounds avoirdupois, instead of apothecaries' units. 
These weights are: for the hot water, 1.03 Ib; for the glass, 0.07 Ib; for 
the ice, 0.89 Ib. 

Our method of finding the quantity of heat absorbed by the ice in 
melting will be to compute the heat lost by the hot water and hot glass 
in cooling to the temperature of the mixture, and from this sum to 
subtract the heat gained by the cold water (melted ice) in warming to 
the mixture temperature. The assumptions involved here are that the 
heat is conserved in the process of mixing and that none of it is gained 
from or lost to any objects except the water, glass and ice. 

(1) The hot water of weight 1.03 Ib and specific heat i Btu/lb F 
cooled from 190 to 53F, the mixture temperature. So it lost a quantity 
of heat HI equal to 

H! = su/&t = 1 77737; X 1.03 Ib X (190 53) F = 141 Btu. 


(2) The glass weighed 0.07 Ib and cooled through the same tempera- 
ture interval as the hot water; its specific heat, as can be seen from 
Black's statement, was half that of water, or 0.5 Btu/lb F. So the heat 
H 2 lost by the glass was 

H 2 = swto = 0.5 -~- X 0.07 Ib X (190 - 53) F = 4.8 Btu. 
Ib F 

(3) The cold water (melted ice) weighed 0.89 Ib and warmed from 
32 to 53 F. So the quantity of heat H$ gained by ic was 

H 3 = swte = i - x 0.89 Ib X (53 - 32) F = 18.7 Btu. 

Ib F 

(4) Let J/4 represent the heat gained by the 0.89 Ib of ice of tempera- 
ture 32F in changing into water of the same temperature. Then it 
follows from our assumption that H i + H% = H 3 + H 4 , or H 4 = 
Hi + H 2 - H 3 = (141 + 4.8 - 18.7) Btu = 127 Btu. 


Thus the value for the heat of fusion of ice yielded by this experiment 
is 127 Btu/o.89 Ib, or 143 Btu/lb. 

In this experiment we see Black taking into account the heat capacity 
of the vessel containing the mixture. This had not been done by Brook 
Taylor, Fahrenheit, or any previous experimenter. 

The result of this experiment coincides sufficiently with that of the 
former; the difference [between the values 139 and 143 Btu/lb] is not 
larger than what may be expected in similar experiments, and might 
arise from the accident of the central parts of the mass of ice being one 
or two degrees colder than its surface. 

These two experiments, and the reasoning which accompanies them, 
were read by me in the Philosophical Club, or Society of Professors and 
others in the University of Glasgow, in the year 1762, and have been 
described and explained in my lectures, there and in Edinburgh, every 
year since. . . . 

It is, therefore, proved that the various phenomena attending the melt- 
ing of ice are inconsistent with the common opinion previously held on 
this subject, and that they support the one which I have proposed. . . . 

In the ordinary process of freezing water, the extrication and emer- 
gence of the latent heat, if I may be allowed to use these terms, is per- 
formed by such minute steps, or rather with such a smooth progress, 
that many may find difficulty in apprehending it; but I shall now men- 
tion another example in which this extrication of the concealed heat be- 
comes manifest and striking. 

This example is an experiment, first made by Fahrenheit [Philosophi- 
cal Transactions of the Royal Society, vol. 33 (1724), P- 7 8 L but since re " 
peated and confirmed by many others. He wished to freeze water from 
which the air had been carefully expelled. This water was contained in 
a small glass globe, about one-third filled, and sealed to prevent the re- 
turn of the air into it. The globe was exposed to the air in frosty weather 
until he felt satisfied that it had cooled down to the temperature of the 
air, which was 6 or 7 Fahrenheit degrees below the freezing point of 
water. The water, however, still remained liquid, so long as the globe 
was left undisturbed; but, when the globe was taken up and shaken a 
litde, the water instantly solidified. 

Others have since found that the experiment will succeed even when 
the water is not deprived of its air, and that the most essential circum- 
stances are that it be contained in a vessel of small size and preserved 
carefully from the least disturbance ... In these circumstances, it may 
be cooled to 6, 7, or 8 degrees below the freezing point without being 
frozen. But, if it be then disturbed, there is a sudden solidification, not 
of the whole, but of a small part only; this forms into feathers of ice, 
traversing the water in every direction and forming a spongy contexture 
of ice, that contains the water in its vacuities, so as to give to the whole 
the appearance of being frozen. But the most remarkable fact is that, 

146 CASE 3 

while this happens (and it happens in a moment of time), this mixture 
of ice and water suddenly becomes warmer, and a thermometer im- 
mersed in it indicates a rise to the freezing point. 

Nothing can be more inconsistent with the old opinion concerning the 
cause of congelation than the phenomena of this experiment. It shows 
that the loss of a little more heat, after the water is cooled down to the 
fp-ezing point, is not the most necessary and inseparable cause of its 
correlation, since the water can be cooled 6, 7, or 8 degrees below that 
point without being congealed. 

This phenomenon, in which a liquid is cooled to a temperature below 
its ordinary freezing point, is now known to be exhibited by many 
substances in addition to water. The under cooled liquid is unstable; it 
will Immediately begin to solidify if disturbed, or if even the tiniest 
crystal of the solid is dropped into it. As Black indicates, this phenome- 
non of undercooling provides a striking example of the "latent heat" 
evolved when a solid freezes; the undercooled liquid retains this heat 
in latent form until solidification starts, and then gradually releases it 
as the solidification proceeds. It is this released heat that warms the 
substance up to its ordinary freezing temperature. 

In addition to his measurements of the heat absorbed by melting ice, 
Black performed the converse experiment of measuring the heat released 
by the resulting water upon freezing. The thought of making this im- 
portant experiment occurred to him during the summer of 1761; but, 
"as there was no ice house then in Glasgow, he waited with impatience 
for the winter, and in December . . . made the decisive experiment." 
The quantities absorbed and released turned out to be equal, which 
convinced him of the soundness of his conjecture that the large amount 
of heat absorbed during melting is not destroyed, but remains latent 
and can be completely recovered from the liquid by freezing it. In 
other words, he could now confidently extend the principle of con- 
servation of heat to include this latent heat as well as sensible heat. 
Indeed, it is only by assuming the validity of the principle in this ex- 
tended form that one is able to calculate heats of fusion from experi- 
ments made either by the method of mixtures or by the method of 
constant heat supply. 

Black also studied the melting of other substances than ice, but did 
not describe them in his lectures; for, as Robison says, "in this elemen- 
tary course, intended for the instruction of the uninformed hearer, he 
chose to confine his proofs to the most familiar observations." At 
Black's request, Irvine determined the heats of fusion of beeswax, 
spermaceti, and tin. For tin the heat of fusion is 26 Btu/lb, this there- 
fore being the quantity of heat required to convert i Ib of solid tin at 
450F (its melting point) to liquid tin of the same temperature. 



When we heat a large quantity of liquid In a vessel, In the ordinary 
manner, by setting it on the fire, we have an opportunity to observe t>ome 
phenomena that are very instructive. The liquid gradually warms, and 
at last attains that temperature which it cannot pass without assuming 
the form o vapor. In these circumstances, we always observe that the 
water Is thrown into violent agitation, which we call boiling. This agita- 
tion continues as long as we keep adding heat to the liquid, and its 
violence increases with the celerity with which the heat is supplied. 

Another peculiarity attends this boiling of liquids which, when first 
observed, was thought very surprising. However long and violently we 
boil a liquid, we cannot make it in the least hotter than when it began 
to boil The thermometer always points at the same degree, namely, the 
vaporific point of that liquid. Hence the vaporific point of a liquid is 
often called its boiling point. 

When these facts and appearances were first observed, they seemed 
surprising, and different opinions were formed with respect to the 
causes on which they depend. Some thought that this agitation was oc- 
casioned by that part of the heat which the water was incapable of re- 
ceiving, and which forced Its way through, so as to occasion the agitation 
of boiling. Others imagined that the agitation proceeded from the air 
which water is known to contain and which is expelled during 
boiling. . . . 

A more just explanation will occur to any person who will take the 
trouble to consider this subject with patience and attention. In the ordi- 
nary manner of heating water, the source of heat is applied to the lower 
parts of the liquid. If the pressure on the surface of the water [such as 
that due to the atmosphere] be not increased, the water will soon acquire 
the highest temperature that It can attain without assuming the form of 
vapor. Any subsequent addition of heat must therefore convert into 
vapor that part of the water which it enters. As this added heat all 
enters at the bottom of the liquid, elastic vapor [steam] Is constantly 
produced there, which, because it weighs almost nothing, must rise 
through the surrounding water and appear to be thrown up to the sur- 
face with violence, and from thence it is diffused through the air. The 
water is thus gradually wasted away, as the boiling continues, but its 
temperature is never increased, at least in that part which remains after 
long-continued and violent boiling. The parts, indeed, in contact with 
the bottom of the vessel may be supposed to have received a little more 
heat, but this Is instandy communicated to the surrounding water 
through which the steam rises. 

This has the appearance of being a simple, plain, and complete account 
of the production of vapor and the boiling of liquids; and it is the only 
account that was given of this subject before I began to deliver these 
lectures. But I am persuaded that it is by no means a full account. It used 
to be taken for granted that, after a liquid was heated up to its boiling 

148 CASE 3 

point, nothing further was necessary but the addition of a little more 
heat to change it into vapor. It was also supposed that when this vapor 
was so far cooled as to be ready for condensation, this condensation, or 
return to the liquid state, would happen at once, in consequence of the 
vapor's losing only a very small quantity of heat. 

But I can easily show, in the same manner as in the case of liquefaction, 
that a very large quantity of heat is necessary for the production of vapor, 
although the body be already heated to that temperature which it cannot 
pass, by the smallest possible degree, without being so converted. The 
undeniable consequence of this, if the old view were correct, should be 
an explosion of the whole water with a violence equal to that of gun- 
powder. But I can show that this large quantity of heat enters into the 
vapor gradually, while it is forming, without making this vapor hotter. 
Thus steam, if examined with a thermometer, is found to have exactly 
the same temperature as the boiling water from which it arose. The 
water must be raised to a certain temperature [2i2F] because at that 
temperature only, is it disposed to absorb heat [that becomes latent]; 
and it is not instantly exploded, because, in that instant, there cannot 
be had a sufficient supply of heat throughout the whole mass. 

On the other hand, I can show that when the steam is condensed back 
into water, the very same large quantity of heat comes out of it into the 
colder, surrounding matter by which it is condensed; and the water into 
which it is changed does not become sensibly colder by the loss of this 
large quantity of heat. , . . 

In the ordinary course of such experiments in this climate, it requires 
about six times the number of minutes to boil of? a small quantity of 
water that it takes to bring it [from room temperature] to the boiling 
point. I can scarcely remember the time in which I had not some con- 
fused idea of this disagreement of the fact with the common opinion; 
and I presume that it has come across the mind of almost every person 
who has attended to the boiling of a pot or pan. But the importance of 
the surmise never struck me with due force till after I had made my 
experiments on the melting of ice. The regular procedure in that case, 
and its similarity to what appears here, encouraged me to expect a 
similar regularity in the boiling of water, if my conjecture was well 
founded. But it appeared to me difficult, if at all possible, to procure a 
source of heat that would be tolerably uniform, or to ascertain its irregu- 
larities. And this discouraged me from making an experiment that would 
in all probability be so anomalous. But I was one day told by a practical 
distiller that, when his furnace was in good order, he could tell to a 
pint what quantity of liquor he would get in an hour. I immediately set 
about boiling off small quantities [weights] of water, and I found that 
it was accomplished in times very nearly proportional to these quanti- 
ties, even although the fire was sensibly irregular. 

I, therefore, set seriously about making experiments, conformable to 
the suspicion that I entertained concerning the boiling of liquids. My 


conjecture, when put into form, was to this purpose. I imagined that, 
during the boiling, heat is absorbed by the water and enters into the 
composition of the steam produced from it, in the same manner as it is 
absorbed by ice in melting and enters into the composition of the re- 
sulting water. And, as the ostensible effect of the heat in this latter case 
consists, not in warming the surrounding bodies, but in converting the 
ice into water; so, in the case of boiling, the heat absorbed does not warm 
surrounding bodies, but converts the water into steam. In both cases, 
considered as the cause of warmth, we do not perceive its presence: it is 
concealed, or latent, and I gave it the name of LATENT HEAT, 

I shall now describe a few of the experiments, which, I apprehend, 
will fully establish the justice of my conjecture. 

Experiment I. I procured some cylindrical tin-plate vessels, about 4 or 
5 inches in diameter, and flat bottomed. Putting a small quantity of water 
into them, of temperature 50?, I set them upon a red-hot kitchen table 
that is, a cast-iron plate with a furnace of burning fuel below it 
taking care that the fire should be pretty regular. After 4 minutes ^the 
water began sensibly to boil, and in 20 minutes more, it was all boiled 
off. This experiment was made on 4th October 1762. . . . 

I reasoned from it in the following manner. The temperature rose 162 
Fahrenheit degrees in 4 minutes, or 40% degrees each minute. Therefore, 
on the assumption that the heat entered the water equally fast during the 
whole ebullition, we must suppose that the quantity of heat absorbed by 
the water, and contained in its vapor, was equivalent to that which would 
raise the temperature of water through 40/2 X 20, or 810 degrees. [This 
is equivalent to saying that 810 Btu were absorbed by each pound of 
water boiled away.] Since this vapor [steam] is no hotter than boiling 
water, the heat is contained in it in a latent state. Its presence is sufficiently 
indicated, however, by the vaporous or expansive form which the water 
has now acquired. 

In experiments 2 and 3 [the descriptions of which we are omitting 
here], the quantities of heat absorbed, and rendered latent, seem to be 
about 830 and 750 [Btu/lb] . . . There are reasons for believing that 
this smallest value resulted from an irregularity in the fire. Upon the 
whole, the conformity of these results with my conjecture was sufficient 
to confirm me in my opinion of its justice. In the course of further ex- 
periments made both by myself and by some friends, and in which the 
utmost care was taken to procure uniformity in the rate at which the 
heat was applied, the absorption was found extremely regular, and 
amounted at an average to about 810 [Btu/lb]. . . . 

From this work on vaporization emerged the conception of still 
another new physical quantity the heat of vaporization of a sub- 
stance, symbol h v . It is defined as the quantity of heat required to 
vaporize unit weight of a liquid without any change of temperature 

150 CASE 3 

taking place. The modern value for the heat of vaporization o water 
is 970 Btu/lb. 

Robison, in his Preface to volume I, says that Black taught the doc- 
trine of latent heat of vaporization in 1761, "before he had made a single 
experiment on the subject ... He thought that what we may observe 
every day was sufficient for settling the main questions." Seeing that 
there was much in common between the phenomena of melting and 
of vaporization, he was able to form his ideas of latent heats of vapor- 
ization by analogy with those developed earlier for melting. But he de- 
layed making quantitative experiments for about a year because he 
thought it would be difficult to obtain a steady source of heat (p. 148) . 

In the experiments that finally were made, he was assisted, first by 
Irvine, and then by James Watt. Robison says: "Fortunately for Dr, 
Black, and for the world, he had now gotten a pupil who was as keenly 
interested in this scientific question as the Professor. This was Mr. 
James Watt, then employed in fitting up the instruments in the 
McFarlane Observatory of the University ... He chanced to have in 
his hand, for repairs, a model of Newcomen's steam engine, belonging 
to the Natural Philosophy Class, and was delighted with the oppor- 
tunity which this small machine gave him for trying experiments con- 
nected with the theory of ebullition, which he had just learned from 
Dr. Black . . . This gentleman, attached to Dr. Black by every tie of 
respect, esteem and affection, supplied him with proofs and illustra- 
tions in abundance, of all the points on which the Professor wanted 
information. These were always recited in the class, with the most 
cordial acknowledgment of obligation to Mr. Watt." 

Concerning Theories of Heat 

Heat is plainly something extraneous to matter. It is either something 
superadded to ordinary matter or some alteration of it from its most 
spontaneous state. Having arrived at this conclusion, it may perhaps be 
required of me, in the next place, to express more distinctly this some- 
.hing to give a full desciiption, or definition, of what I mean by the 
word heat in matter. This, however, is a demand that I cannot satisfy 
entirely. I shall mention, by and by, the supposition relating to this sub- 
ject that appears to me the most probable. But our knowledge of heat 
is not brought to that state of perfection that might enable us to propose 
with confidence a theory of heat or to assign an immediate cause for it. 

Some ingenious attempts have been made in this part of our subject, 
but none of them has been sufficient to explain the whole of it. How- 
ever, this should not give us much uneasiness. It is not the immediate 
manner of acting, dependent on the ultimate nature of this peculiar sub- 
stance, or this particular condition of common matter, that most interests 
us. We are far removed as yet from that extent of chemical knowledge 


which makes this a necessary step for further improvement. We have 
still before us an abundant field of research in the various general facts 
and laws of action, which constitute the real objects of pure chemical 
science. And I apprehend that it is only when we have nearly completed 
this catalogue that we shall have a sufficient number of resembling facts 
to lead us to a clear knowledge of the behavior peculiar to this substance 
or modification of matter called heat; and, when we have at last attained 
it, I presume that the discovery will not be chemical but mechanical. It 
would, however, be unpardonable to pass without notice some of the 
most ingenious attempts which have had a certain currency among the 
philosophical chemists. 

The first attempt I think was made by Lord Verulam [Francis Bacon, 

in 1620]; next after him, Mr. Boyle [Robert Boyle, in 1665 and 1673] 

-gave several dissertations on heat; and Dr. Boerhaave, in his lectures on 

chemistry [1732], endeavored to prosecute the subject still further, and 

to improve on the two former authors. 

Lord Verulam's attempt may be seen in his treatise De forma Cahdi 
[1620], which he offered to the public as a model of the proper manner 
of prosecuting investigations in natural philosophy. In this treatise he 
enumerated all the principal facts then known about heat and its pro- 
duction, and endeavored, after a cautious and mature consideration of 
these, to form some well-founded opinion of its cause. 

The only conclusion, however, that he was able to draw from the whole 
of his facts is a very general one, namely, that heat is motion. This con- 
clusion was founded chiefly on the consideration of several means by 
which heat is produced, or made to appear, in bodies, such as the per- 
cussion of iron, the friction of solid bodies, the collision of flint and 

The first of these examples is a practice to which blacksmiths have 
sometimes recourse for kindling a fire; they take a rod of soft iron, half 
an inch or less in thickness, and, laying the end of it upon their anvil, 
turn and strike that end very quickly on its different sides with a ham- 
mer; it very soon becomes red hot and can be employed to kindle shav- 
ings of wood or other very combustible matter. The heat producible by 
the strong friction of solid bodies occurs often in some parts of heavy 
machinery when proper care has not been taken to diminish that friction 
as much as possible by the interposition of lubricating substances. Thick 
forests are said to have taken fire sometimes because of the branches rub- 
bing one another in stormy weather. Savages in different parts of the 
world have recourse to the friction of pieces of wood for kindling their 

In all these examples, heat is produced or made to appear suddenly in 
bodies that have not received it in the usual way of communication from 
others, the only cause of its production being a mechanical force or im- 
pulse, or mechanical violence. It was, therefore, very natural for Lord 
Verulam to conclude that the most usual, nay, perhaps the sole effect 

152 CASE 3 

of mechanical force or impulse applied to a body is to produce some sort 
of motion of that body. 

Although this eminent philosopher has had a great number of follow- 
ers on this subject, his opinion has been adopted with two different 
modifications. The greater number of the English philosophers suppose 
this motion to be in the small particles of the heated bodies, and imagine 
that it is a rapid tremor, or vibration, of these particles among one an- 
other. Mr. Macquer and Mons. Fourcroy both incline, or did incline, to 
this opinion. I acknowledge that I myself cannot form a conception of 
this internal tremor which has any tendency to explain even the more 
simple effects of heat, and I think that Lord Verulam and his followers 
have been contented with very slight resemblances indeed between those 
most simple effects of heat and the legitimate consequences of a tremu- 
lous motion. I also see many cases in which intense heat is produced in 
this way, but where I am certain that the internal tremor is incomparably 
less than in other cases of percussion, similar in all other respects. Thus 
the blows that make a piece of soft iron intensely hot produce no [easily 
observable] hotness in a similar piece of very elastic steel. 

But the greater number of French and German philosophers, and Dr. 
Boerhaave, have held that the motion of which they suppose heat to con- 
sist is not a tremor, or vibration, of the particles of the hot body itself, but 
of the particles of a subtle, highly elastic, and penetrating fluid matter, 
which is contained in the pores of hot bodies, or interposed among their 
particles a matter that they imagine to be diffused through the whole 
universe, pervading with ease the densest bodies. Some suppose that 
this matter, when modified in different ways, produces light and the 
phenomena of electricity. 

But neither of these suppositions has been fully and accurately con- 
sidered by their authors, or applied to explain the whole of the facts and 
phenomena relating to heat. They have not, therefore, supplied us with 
a proper theory or explication of the nature of heat. 

A more ingenious attempt has lately been made, the first oudines of 
which, so far as I know, were given by the late Dr. Cleghorn, in his 
inaugural dissertation on the subject of heat, published here [at the Uni- 
versity of Edinburgh, in 1779]. He supposed that heat depends on the 
abundance of that subtle elastic fluid which had been imagined before by 
other philosophers to be present in every part of the universe and to be 
the cause of heat. But these other philosophers had assumed, or supposed, 
one property only as belonging to this subtle matter, namely, its great 
elasticity, or strong repulsion of its particles for one another; whereas, 
Dr. Cleghorn has supposed it to have still another property, namely, a 
strong attraction for the particles of the other kinds of matter in nature, 
which have in general more or less [gravitational] attraction for one an- 
other. Thus he supposed that the ordinary kinds of matter consist of 
particles having a strong attraction both for one another and for the 
matter of heat; whereas the subtle elastic matter of heat is self-repelling, 


its particles having a strong repulsion for one another while they are at- 
tracted by the other kinds of matter, and that with different degrees of 
force. . . . 

Such an idea of the nature of heat is the most probable of any that I 
know; and an ingenious attempt to make use of it has been published by 
Dr. Higgins, in his book on vegetable acid [any organic acid] and other 
subjects. It is, however, altogether a supposition. 

In passages not included here, Black says that his discovery that 
different substances have different capacities for heat are very unfavor- 
able to the opinion that heat is "a tremulous, or other, motion of the 
particles of matter." If that theory were correct, he contends, then the 
more dense substances ought to have the larger specific heats, whereas 
in many cases this is not true; for instance, mercury is more dense than 
water, but has a much smaller specific heat. "I do not see how this 
objection can be evaded." 

More than half a century elapsed before it became clear that this 
objection of Black's is invalid and can be evaded; but to see this re- 
quired a much better knowledge of the weights and velocities of the 
particles (atoms and molecules) of different substances than was 
available in his day. 

In another place Black points out how the fact that bodies expand in 
volume when heated had led many to suppose that the addition o 
heat to a body increased its weight. He reviews experiments made by 
Boerhaave, Buffon, Whitehurst ("who is distinguished by his accuracy 
and ingenuity in the construction of very nice and delicate balances"). 
Roebuck (who "made his experiments with the most scrupulous 
accuracy") and, lastly, Dr. Fordyce (see Sec. 3). Although finding the 
results of these various experiments to be contradictory, he concludes 
"that if heat depends on the presence of a subtle matter introduced into 
bodies, this matter lacks any perceptible degree of gravitation." 

It has not, therefore, been proved by any experiment that the weight 
of bodies is increased by their being heated, or by the presence of heat 
in them. This may be thought very inconsistent with the idea of the 
nature or cause of heat that I lately mentioned as the most plausible: 
I mean the notion that heat depends on the abundance of a subtle mat- 
ter highly elastic, or self-repellent which easily enters into all bodies 
and penetrates them throughout, being strongly attracted by the matter 
of those bodies. It must be confessed that the afore-mentioned fact may 
be stated as a strong objection against this supposition. 

Some have attempted to remove this objection by supposing the mat- 
ter of heat to be so subtle and tenuous that no quantity of it which we 
can collect together can have any sensible weight. Others have thought 
that it might be the matter which causes the gravitation of other bodies 

154 CASE 3 

and so could not be supposed to gravitate like them, but, on the contrary, 
might have an opposite tendency. 

These attempts to remove the objection are ingenious, but they are 
not satisfactory. We find too much difficulty in attempting to compre- 
hend them. And this has contributed more than any direct arguments 
to confirm in their opinion those who, with Lord Verulam, assert that 
heat ... Is not a material substance, transferable from one body to an- 
other, but a mere state or condition in which the matter comprising all 
bodies may be found. Yet, notwithstanding this difficulty, I imagine that, 
as we proceed, you will find yourselves more and more impressed with 
the belief that heat is the effect of a peculiar substance. . . . 

When we perceive that what we call heat disappears in the liquefaction 
of ice, and reappears in the congelation of water, and a number of anal- 
ogous phenomena, we can hardly avoid thinking it a subtance that may 
be united with the particles of water in the same manner as [for example] 
the particles of Glauber's salt [sodium sulfate] are united with them in 
solution, and may be separated as these are. But, since heat has never 
been observed by us in a separate state, all our notions of this union must 
be hypothetical. Moreover, this hypothesis must be combined with some 
other hypothesis concerning the unions of those other substances; for it 
must be acknowledged that our notions of those more palpable and 
familiar combinations are all hypothetical. We think that we can con- 
ceive how a particle of common salt can draw around it, and attach to 
itself, particles of water, and how they may adhere and compose a saline 
crystal. We transfer this notion to the relation between bodies and heat 
and without much reflection, or distinct conception suppose that, 
in like manner, a particle of a body attaches itself to a number of par- 
ticles of heat. Heat is, therefore, supposed to be somehow contained or 
lodged in the pores of bodies, and we endeavor to account for observable 
changes in bodies, such as increase of volume, or fusion, or vaporization, 
by showing some resemblance between these appearances and those that 
occur in chemical unions or mixtures. 

Many have been the speculations and views of ingenious men about 
this union of bodies with heat. But, as they are all hypothetical, and as 
the hypothesis is of the most complicated nature, being in fact a hypo- 
thetical application of another hypothesis, I cannot hope for much useful 
information by attending to it, A nice adaptation of conditions will make 
almost any hypothesis agree with the phenomena. This will please the 
imagination, but does not advance our knowledge. I therefore avoid such 
speculations, as taking up time which may be better employed in learn- 
ing more of the general laws of chemical operations. . . . 

The Idea that heat might be a material substance stems from the 
Greeks, and so Is much older than Black indicates. It was invoked by 
Robert Boyle (Essays of Effluviums, 1673) in an attempt to explain 
the gain in weight shown by metals on calcination. In the eighteenth 


century it came into general use, and indeed proved to be much more 
helpful in explaining the thermal phenomena known at that time than 
was the rival and relatively undeveloped view that heat is something 
associated with the motions of the particles of ordinary matter. 

In 1779, William Cleghorn, who is mentioned by Black (p. 152), 
extended the material theory to take into account Black's discoveries of 
specific and latent heats. The main properties that Cleghorn and later 
investigators ascribed to "matter of heat" or "caloric," as Lavoisier 
called it in 1787 may be summarized for our purposes in the form of 
"postulates of the caloric theory" as follows: 

(i) Caloric is an elastic fluid, the particles of which repel one an- 
other strongly. 

(ii) The particles of caloric are attracted by the particles of ordinary 
matter, the magnitude of the attraction being different for different 
substances and for different states of aggregation. 

(iii) Caloric is indestructible and uncreatable. (This "principle of 
conservation of heat" was from the first regarded as plausible; for, from 
the time of the Greeks onward, the idea had existed that matter was 
indestructible and, if heat were matter, then it ought to be indestruct- 
ible. But with the development of the method of mixtures and also of 
the concept of latent heat, this postulate became an indispensable part 
of the caloric theory.) 

(iv) Caloric can be either sensible or latent, and in the latter state is 
combined "chemically" with the particles of matter to form the liquid 
or vapor. (Sensible caloric, which increases the temperature of a body 
to which it is added, was supposed to form an "atmosphere" around 
the particles of the body. But latent caloric supposedly was combined 
with these particles in a manner similar to the chemical combinations 
of particles (atoms) themselves; this supposedly produced a new com- 
pound the liquid or the vapor and took place, as do ordinary 
chemical reactions, only in definite proportions and under definite 

(v) Caloric does (does not) have appreciable weight (see Sec. 3) . 


Count Rumford (1753-1814), whose family name was Benja- 
min Thompson, carried out an experimental study of "the weight 
ascribed to heat" as part of an extensive program of research designed 
by him primarily to throw light on the question of the ultimate nature 
of heat. 

156 CASE 3 

Although Rumford was tremendously versatile and gained interna- 
tional fame as a philanthropist, administrator, and authority on military 
problems, his most consuming interest and perhaps greatest skill lay 
in physical experimentation, especially in the field of heat. Of this 
interest, he wrote, in his Memoire sur la Chaleur (1804) : 

To engage in experiments on heat was always one of my most agree- 
able employments. This subject had already begun to excite my attention, 
when, in my seventeenth year, I read Boerhaave's admirable Treatise on 
Fire. Subsequently, indeed, I was often prevented by other matters from 
devoting my attention to it, but whenever I could snatch a moment I re- 
turned to it anew, and always with increased interest. Even now this 
object of my speculations is so present to my mind, however busy I may 
be with other affairs, that everything taking place before my eyes, having 
the slightest bearing upon it, immediately excites my curiosity and at- 
tracts my attention. 

In Rumford's time, the caloric, or material, theory of heat was well 
established and generally accepted by most scientists. Indeed, as a con- 
ceptual scheme serving to correlate most of the facts then known about 
heat, and as a convenient way to think about these facts or even to 
predict new ones, it was proving itself to be far more useful than the 
opposing and then relatively undeveloped doctrine that heat is a form 
of motion. Rumford, however, came to regard the mode-of-motion 
view as basically the sounder one, and he continually reiterated this 
belief in many of the 72 papers and essays which he wrote on a wide 
variety of subjects. Most of his experiments were concerned with 
thermal phenomena and, in devising them, his primary object was to 
try to attack the caloric theory from as many different points of view 
as seemed possible. 

According to the caloric theory (p. 155), heat was a material substance. 
Now, material substance, or matter, is ordinarily defined as that which 
occupies space and has weight. Hence, if heat were matter, in the ordi- 
nary sense of the word, it should have weight that is, it should be 
attracted gravitationally by the earth as well as by the particles of all 
other matter. 

Attempts to detect this weight ascribed to heat had been made at 
various times during the eighteenth century by a number of excellent 
experimenters. Up to about 1776, the experiments were carried out 
with solid metals, such as iron, copper, g,,ld, and silver. The usual pro- 
cedure was to weigh the metal when it was cold and then when it was 
hot usually red-hot, or even white-hot, so that the quantity of heat 
added would be large. The results varied widely. In some cases the 
metal appeared to weigh more when cold; in other cases, to weigh 


more when hot; in a few cases, not to change in weight. That the 
results were conflicting is not surprising, in view of the difficult char- 
acter of such experiments. Although good balances for weighing were 
available, there are many other possible sources of error when the same 
object is weighed at widely different temperatures. Moreover, the 
methods that had to be used to heat the metals were crude. For in- 
stance, one experimenter heated his metal in charcoal by means of a 
candle and a blowpipe. 

Most of these early experimenters were aware that the effects which 
they had observed might be due, not to any supposed weight of heat, 
but to accidental factors, such as a current of air rising above the hot 
metal (a convection current - , as it later came to be called), or a difference 
in the lengths of the two balance arms resulting from thermal expan- 
sion, or a chemical change occurring in the heated metal. For instance, 
when a piece of iron is heated in air, loose flakes of iron oxide form 
on its surface and may fall off during the course of the experiment. 

In the last quarter of the century, the modes of attack on this prob- 
lem began to be influenced by Joseph Black's discoveries of specific and 
latent heats (Sec. 2). Black had found, for one thing, that the quantity 
of heat needed to change i Ib of ice at 32F into water at the same 
temperature is equal to that which must be added to i Ib of water to 
raise its temperature through 141 (now known to be more nearly 144) 
Fahrenheit degrees. This suggested that, if heat did have weight, it 
might be easier to detect it by melting or freezing a substance, for then 
the quantity of heat added or subtracted would be much larger than 
in the earlier experiments in which solid metals were merely changed 
in temperature. In truth, some experiments of this kind had been 
made nearly a century earlier by Robert Boyle, who reported in his 
New Experiments and Observations Touching Cold (1665) that water 
weighed first when frozen and then when unfrozen showed "not one 
grain difference." On the other hand, it was also Boyle who was 
among the first to lend encouragement to the idea that heat might be 
a substance having weight, for, in his Essays of Effluviums (1673), ^ e 
showed that a metal gains weight upon calcination and suggested that 
this might be due to the addition to it of "the material particles of fire." 

In 1785, George Fordyce, a British physician who was acquainted 
with Black's discoveries, carried out careful experiments to determine 
whether there was any change of weight when water is frozen. Fordyce 
put some water in a glass globe, sealed and cleaned the globe, and 
weighed it on a very sensitive balance. He then put the globe in a 
freezing mixture of ice and common salt and, just when the water was 
ready to freeze, removed and dried the globe, and weighed it. Replac- 
ing the globe in the freezing mixture and waiting until some of the 

158 CASE 3 

water had frozen, he again removed and weighed it and found an 
increase in weight of about i part in 129,000. He repeated this procedure 
five times; each time more water had frozen and more weight had 
been gained. When the ice subsequently was allowed to melt, this 
additional weight was gradually lost. 

Count Rumford was much interested in these experiments of 
Pordyce's and in 1787 set out to repeat them. Twelve years later he 
described his results in a paper published in the Philosophical Transac- 
tions of the Royal Society, vol. 89 (1799), p. 179. The edited and 
annotated version that follows is based on this paper as it is reprinted 
in The Complete Worlds of Count Rumford (American Academy of 
Arts and Sciences, Boston, 1870-75), vol. II, pp. 1-16. 


Benjamin Thompson (Count Rumford) 

The various experiments which have hitherto been made with a view to 
determine the question, so long agitated, relative to the weight which 
has been supposed to be gained, or to be lost, by bodies upon their being 
heated, are of a very delicate nature and are liable to many errors, not 
only on account of the imperfections of the instruments used, but also 
because of effects, much more difficult to appreciate, arising from the 
vertical [convection] currents in the atmosphere, caused by the hot or 
cold body which is placed in the balance. It is not at all surprising that 
opinions have been so much divided, relative to a fact so very difficult to 

It is a considerable time since I first began to meditate upon this sub- 
ject, and I have made many experiments with a view to its investigation; 
and in these experiments I have taken all those precautions to avoid 
errors which a knowledge of the various sources of them, and an earnest 
desire to determine a fact which I conceived to be of importance to be 
known, could inspire; but though all my researches tended to convince 
me more and more that a body acquires no additional weight upon being 
heated^ or, rather, that heat has no effect whatever on the weights of 
bodies, I have been so sensible of the delicacy of the inquiry that I was 
for a long time afraid to form a decided opinion upon the subject. 

Being much struck with the experiments recorded in the [Philosophi- 
cal} Transactions of the Royal Society, vol. LXXV [1785], made by Dr. 
Fordyce, on the weight said to be acquired by water upon being frozen; 
and being possessed of an excellent balance, belonging to his Most Serene 
Highness die Elector Palatine Duke of Bavaria; early in the beginning 
of the winter of the year 1787 as soon as the cold was sufficiently in- 
tense for my purpose I set about to repeat those experiments, in order 
to convince myself whether the very extraordinary fact related by Dr. 
Fordyce might be depended on With a view to removing, as far as was 


in my power, every source of error and deception, I proceeded in the 
following manner. 

Having provided a number of glass bottles, of the form and size of 
what in England is called a Florence flask blown as thin as possible 
and of the same shape and dimensions, I chose from amongst them two, 
which, after using every method I could imagine of comparing them, 
appeared to be so much alike as hardly to be distinguished from each 

Into one of these bottles, which I shall call A, I put 4107.86 grains 
[about 0.59 Ib avoirdupois] of pure distilled water, which filled it about 
half full, and into the other, 5, I put an equal weight of weak spirit of 
wine [alcohol]. After sealing both bottles hermetically, I washed them, 
and wiped them perfectly clean and dry on the outside. I then hung 
them from the arms of the balance and placed the balance in a large 
room, which for some weeks had been regularly heated every day by a 
German stove, and in which the air was kept up to the temperature of 
6iF, with very little variation. Having suffered the bottles, with their 
contents, to remain in this situation till I conceived they must have ac- 
quired the temperature of the circumambient air, I wiped them afresh, 
with a very clean, dry cambric handkerchief, and brought them into the 
most exact equilibrium possible, by attaching a small piece of very fine 
silver wire to the arm of the balance holding the lighter bottle. 

Having suffered the apparatus to remain in this situation about 12 
hours longer, and finding no alteration in the relative weights of the 
bottles they continuing all this time to be in the most perfect equilib- 
rium I now removed them to a large uninhabited room, fronting the 
north, in which the air, which was very quiet, was at the temperature of 
29F, the air outdoors being at the same time at 27F; and going out 
of the room, and locking the door after me, I suffered the bottles to re- 
main 48 hours, undisturbed, in this cold room, attached to the arms of 
the balance as before. 

As the expiration of that time, I entered the room using the utmost 
caution not to disturb the balance and, to my great surprise, found that 
bottle A very sensibly preponderated. The water in this bottle was com- 
pletely frozen into one solid body of ice; but the spirit of wine, in bottle 
B, showed no signs of freezing. 

I now very cautiously restored the equilibrium by adding small pieces 
of the very fine wire of which gold lace is made to the arm of the balance 
from which bottle B was suspended, and I found that bottle A had aug- 
mented its weight by 1/35,904 part of Its whole weight at the beginning 
of the experiment. The initial weight of the bottle and contents was 
4811.23 grains (the bottle weighed 703.37 grains), and it now required 
134/1000 part of a grain, added to the opposite arm of the balance, to 
counterbalance it. 

Having had occasion, just at this time, to write to my friend, Sir 
Charles Blagden, upon another subject, I added a postscript to my letter. 

160 CASE 3 

giving him a short account of this experiment, and telling him how 
"very contrary to my expectation" the result of it had turned out; but I 
soon after found that I had been too hasty in my communication. Sir 
Charles, in his answer to my letter, expressed doubts respecting the fact; 
but, before his letter had reached me, I had learned from my own ex- 
perience how very dangerous it is in philosophical investigations to draw 
conclusions from single experiments. 

Having removed the balance, with the two bottles attached to it, from 
the cold to the warm room (which still remained at the temperature of 
6rF), I waited until the ice in bottle A had been totally reduced to 
water and had acquired the temperature of the surrounding air. The two 
bottles, after being wiped perfectly clean and dry, were found to weigh 
as at the beginning of the experiment, before the water was frozen. 

This experiment, being repeated, gave nearly the same result the 
water appearing when frozen to be heavier than in its liquid state. But 
some irregularity in the manner in which the water lost this additional 
weight when it was afterward thawed, and also a sensible difference in 
the weight apparently acquired in the different trials, led me to suspect 
that the experiment could not be depended on for deciding the fact in 
question. I therefore set about to repeat it, with some variations and im- 
provements. But before I give an account of my further investigations 
relative to this subject, it may not be amiss to mention the method I pur- 
sued for discovering whether the appearances mentioned in the fore- 
going experiments might not arise from the imperfections of my balance. 

My suspicions respecting the accuracy of the balance arose from a 
knowledge which I acquired from the maker of the manner in 
which it was constructed. The three principal points of the balance having 
been determined, as nearly as possible, by measurement, the axes of mo- 
tion were firmly fixed in their places, in a straight line. After the beam 
was finished and its two arms brought into equilibrium, the balance was 
proved [tested] by hanging weights, which were known to be exactly 
equal, from the ends of its arms. 

If with these weights the balance remained in equilibrium, this was 
considered as a proof that the beam was just; but if one arm was found 
to preponderate, the other was gradually lengthened, by beating it upon 
an anvil, until the difference of the lengths of the arms was reduced to 
nothing, or until the balance remained in equilibrium when equal 
weights were suspended from the two arms. Care was taken before each 
trial to bring the two ends of the beam into equilibrium by reducing with 
a file the thickness of the arm that had been lengthened. 

By this method of constructing balances one may obtain the most 
perfect equality in the lengths of the arms, and consequently the greatest 
possible accuracy, especially if the balance is used at a time when the 
temperature of the air is the same as when the balance was made. But 
it may have happened that, in order to bring the arms of the balance to 
the same length, one of them had to be hammered much more than the 


other, and I suspected that the texture of the metal forming the two 
arms might possibly be rendered so far different by this operation as to 
occasion a difference in their amounts of expansion when heated. This 
difference might occasion a sensible error in the balance when, being 
charged with a large weight, it should be exposed to a considerable change 
of temperature. 

To determine whether the apparent augmentation of weight in the 
afore-mentioned experiments arose in any degree from this cause, I had 
only to repeat the experiment, causing the two bottles A and B to ex- 
change places upon the arms of the balance; but, as I had already found a 
sensible difference in the results of different repetitions of the same ex- 
periment, made as nearly as possible under the same circumstances, and 
as it was above all things of importance to ascertain the accuracy of my 
balance, I preferred making a particular experiment for that purpose. 

In a passage omitted here, Rumford says that, in planning this test 
of the balance, his first idea had been to use two equal glass globes, 
filled with mercury. But he feared that, despite all his precautions, 
moisture had deposited on the glass flasks in the preceding experi- 
ments. So he decided to use two equal, solid brass globes, "well gilt 
and burnished"; for he had previously found that moisture did not 
deposit on a metal surface that had been gilded. 

Having suspended these brass globes from the two arms of the 
balance by fine wires, he let them stand for a day in the room at 6iF, 
then carefully balanced them and, finally, removed them to a room at 
26 F, where they were left all night. 

The result of this trial furnished the most satisfactory proof of the 
accuracy of the balance; for, upon entering the cold room, I found the 
equilibrium as perfect as at the beginning of the experiment. Having 
thus removed my doubts respecting the balance, I now resumed my in- 
vestigations relative to the augmentation of weight which liquids have 
been said to acquire upon being frozen. 

In my experiments, I had, as I then imagined, guarded as much as 
possible against every source of error and deception. The bottles being of 
the same size, neither any occasional alteration in the pressure of the 
atmosphere during the experiment, nor the necessary and unavoidable 
difference in the densities of the air in the hot and in the cold rooms in 
which they were weighed, could affect their apparent weights; and their 
shapes and surface areas being the same, and as they remained for such 
a considerable length of time at the high and low temperatures to which 
they were exposed, I flattered myself that the quantities of moisture re- 
maining attached to their surfaces could not be so different as sensibly 
to affect the results of the experiments. But, in regard to this last cir- 
cumstance, I afterwards found reason to conclude that my opinion was 



Admitting the fact stated by Dr. Fordyce and which my experi- 
ments had hitherto rather tended to corroborate than to contradict I 
could not conceive any other cause for the augmentation of the apparent 
weight of water upon freezing than the loss of so large a proportion 
[144 Btu/lb] of its latent heat as that liquid is known to evolve when it 
freezes; and I concluded that, if the loss of latent heat added to the 
weight of one body, it must of necessity produce the same effect on an- 
other, and consequently, that the augmentation of the quantity of heat 
must in all bodies and in all cases diminish their apparent weights. 

Rumford says (p.ifo) that he began these experiments with a tend- 
ency toward the conviction that heat had no effect whatever on the 
weights of objects. Now we find him consciously shifting to the oppo- 
site point of view; he accepts Fordyce's result, which his own experi- 
ment has seemed to confirm, and proceeds to generalize it so as to 
apply to any body heated or cooled in any manner whatever. 

It seems to be a fairly common belief that a well-trained scientist 
always approaches his scientific problems with an entirely open mind 
without preconceived opinions and prejudices. Was Rumford in this 
respect a poor scientist? Or is it possible that no inquiry, of any kind, 
can be planned or gotten under way until some selection of subject 
matter has been made; and that such selection requires some assump- 
tion, or preconception, or prejudice, which both guides the inquiry 
and delimits its subject matter? Is it possible that preconceived opin- 
ions about, say, certain relations may increase our chances of discover- 
ing these relations, if they exist? However, if the answer is in the 
affirmative, certainly we would want to add that the investigator must 
be willing to abandon his preconceived opinions if they are not sup- 
ported by the results of subsequent observation and experiment. 

Having adopted, at least tentatively, the assumption that water gains 
in weight upon, freezing, Rumford next sets out to determine whether 
liquids change in weight when they lose heat merely by cooling, with- 
out freezing. Here he is returning to a method similar to that em- 
ployed by the early eighteenth-century experimenters (p. 156). But 
again the work of Black has suggested an improved and more sensitive 
test. Instead of weighing a single substance, as did the early experiment- 
ers, Rumford compares the weights, before and after cooling, of two 
substances water and mercury that have widely different specific 

To determine whether this is actually the case or not, I made the fol- 
lowing experiment. Having provided two bottles, as nearly alike as 
possible, and in all respects similar to those made use of irr the preced- 
ing experiments, into one of them I put 4012.46 grains [about 0.57 Ib 


avoirdupois] of water, and into the other an equal weight of mercury. 
Sealing them hermetically and suspending them from the arms of the 
balance, I suffered them to acquire the temperature of my room, 6iF. 
After bringing them into a perfect equilibrium with each other, I re- 
moved them into a room in which the air was at the temperature of 
34 F, where they remained 24 hours. But there was not the least ap- 
pearance of either of them acquiring or losing any weight. 

Here it is very certain that the quantity of heat lost by the water was 
considerably larger than that lost by the mercury, for the specific heats of 
water and mercury have been determined to be to each other as 1000 to 
33; but this difference in the quantities of heat lost produced no sensible 
difference in the weights of tht liquids in question. 

Had any difference of weight really existed, had it been no more than 
one millionth part of the weight of either of the liquids, I should cer- 
tainly have discovered it; and had it amounted to so much as 1/700,000 
part of that weight, I should have been able to have measured it, so sensi- 
tive and so very accurate is the balance which I used in these experiments. 

There is no indication that Rumford repeated this experiment. Surely 
he must have, in view of his earlier comment on "how very dangerous 
it is ... to draw conclusions from single experiments" and because of 
his willingness (expressed in the next paragraph) again to question the 
validity cf his earlier, freezing experiments, which, as we know, he 
repeated at least once. 

This readiness to question the earlier experiments also suggests that 
Rumford actually had not shifted wholeheartedly to Fordyce's view 
that heat had weight. A scientist, such as Rumford, is even In his 
science still a human being. Logical considerations may lead him to 
change to and even act upon a belief that is repugnant to him, but 
wholehearted conversion is difficult because of the emotional factors 

I was now much confirmed in my suspicions that the apparent aug- 
mentation of the weight of the water upon its being frozen, in the ex- 
periments before related, arose from some accidental cause; but I was 
not able to conceive what that cause could possibly be, unless it were 
either a larger quantity of moisture deposited on the external surface of 
the bottle containing the water than on the surface of that containing 
the spirit of wine, or some vertical current or currents of air caused by 
the bottles, or one of them not being exactly at the temperature of the 
surrounding atmosphere. 

I had foreseen and, as I thought, guarded sufficiently against these ac- 
cidents by making use of bottles of the same size and form, which were 
blown of the same kind of glass and at the same time, and by exposing 
them during the experiments for a considerable length of time to the 
different temperatures which alternately they were made to acquire. 

164 CASE 3 

However, I did not know the relative conducting powers of ice and of 
spirit of wine with respect to heat in other words, the degrees of 
facility of difficulty with which they acquire the temperature of the 
medium in which they are exposed, or the time taken up in that opera- 
tion. Consequently, I was not absolutely certain as to the equality of the 
temperatures of the contents of the bottles at the time when their weights 
were compared. So I determined now to repeat the experiments, with 
such variations as should put the matter in question out of all doubt. 

By conduction of heat is meant the transfer of heat from places of 
higher to places of lower temperature, occurring either through a body 
or from one body to another in contact with it, and without any visible 
movement of the parts of the bodies. It is to be distinguished from 
convection, which occurs only in liquids and gases, and in which the 
fluid moves as a result of pressure differences, thus carrying its heat 
with it. The pressure differences may be brought about in many 
different ways; a common cause is the local changes of density that 
result from unequal warming or cooling of the fluid. 

A way to measure the relative rates at which heat is conducted 
through various solid substances was first suggested by Benjamin 
Franklin, and measurements by his method were made in 1789 by 
J. Ingenhausz. But it was Rumford, in an essay published in 1797, who 
showed that water and various other non-metallic liquids are poor con- 
ductors of heat, and that the transfer of heat through them occurs 
mainly by convection. Because of the disturbing effects of convection, 
it is much more difficult to investigate conduction in liquids and gases 
than in solids. 

I was more anxious to assure myself of the real temperatures of the 
bottles and their contents because any difference in their temperatures 
might vitiate the experiment, not only by causing unequal currents in 
the air, but also by causing, at the same time, a larger or smaller quantity 
of moisture to remain attached to the glass. To remedy these evils, and 
also to render the experiment more striking and satisfactory in other 
respects, I proceeded in the following manner. 

Having provided three bottles, A^ B, and C, as nearly alike as possible, 
and resembling in all respects those already described, into the first, A, 
I put 4214.28 grains [about 0.60 Ib avoirdupois] of water and a small 
thermometer, made on purpose for the experiment and suspended in the 
bottle in such a manner that its bulb remained in the middle of the mass 
of water; into the second bottle, B, I put a like weight of spirit of 
wine, with a like thermometer; and into the bottle C I put an equal 
weight of mercury. 

These bottles, being all hermetically sealed, were placed in a large 
room, in a corner far removed from the doors and windows, and where 


the air appeared to be perfectly quiet. After they had remained there for 
more than 24 hours the temperature of the room being kept at 6iF 
during all that time with as little variation as possible the contents of 
bottles A and B appeared, by their inclosed thermometers, to be exactly at 
the same temperature. The bottles were then wiped with a very clean, dry, 
cambric handkerchief and were afterwards suffered to remain exposed to 
the free air of the room a couple of hours longer, in order that any in- 
equalities in the quantities of heat or of the moisture attached to their 
surfaces, which might have been occasioned by the wiping, would be 
corrected by the operation of the atmosphere by which they were sur- 
rounded. Then all were weighed, being brought into the most exact 
equilibrium with each other by attaching small pieces of very fine silver 
wire to the necks of those bottles that were the lighter. 

This being done, the bottles were taken to a room in which the air was 
at 30 F. Bottles A and B were hung from the arms of the balance, and 
bottle C was hung, at an equal height, from the arm of a stand con- 
structed for that purpose and placed as near the balance as possible, a 
very sensitive thermometer being suspended beside it. 

At the end of 48 hours, I reentered the room, opening the door very 
gently for fear of disturbing the balance. I had the pleasure of finding 
that the three thermometers (that in bottle A was now inclosed in a 
solid cake of ice) all stood at the same point, 29 F, and that bottles A 
and B remained in the most perfect equilibrium. 

To assure myself that the play of the balance was free, I now ap- 
proached it very gently and caused it to vibrate; and I had the satisfac- 
tion of finding, not only that it moved with the utmost freedom, but 
also, when its vibration ceased, that it rested precisely at the point from 
which it had set out. 

I now removed bottle B from the balance, and put bottle C in its place; 
and I found that it likewise had the same apparent weight as at the be- 
ginning of the experiment, being in the same perfect equilibrium with 
bottle A as at first. 

I afterwards removed the whole apparatus into a warm room and, 
causing the ice in bottle A to thaw, let the three bottles remain there till 
they and their contents had acquired the exact temperature of the sur- 
rounding air. I then wiped them very clean and, comparing them, found 
that their weights remained unaltered. 

This experiment I afterwards repeated several times, and always with 
precisely the same result the water in no instance appeared to gain, or 
to lose, the least weight upon being frozen or upon being thawed; nor 
were the relative weights of the liquids in either of the other bottles in 
the least changed by the various temperatures to which they were exposed. 

If the bottles were weighed at a time when their contents were not 
precisely of the same temperature,, they would frequently appear to have 
gained, or to have lost, some weight; but this doubtless was due to the 
vertical [convection] currents which they produced in the atmosphere 

166 CASE 3 

upon being heated or cooled in it, or to unequal quantities of moisture 
attached to the surfaces of the bottles, or to both these causes operating 

As I knew that the conducting power of mercury with respect to heat is 
considerably larger than that of either water or spirit of wine, while its 
specific heat is much less than that of either of them, I did not think it 
necessary to inclose a thermometer in the bottle C, which contained the 
mercury; for it was evident that, when the contents of the other two 
bottles should appear, by their thermometers, to have arrived at the tem- 
perature of the medium in which they were exposed, the contents of the 
bottle C could not fail to have acquired it also, and even to have arrived 
at it before them; for the time needed to heat or to cool any body increases, 
caeteris pan bus, directly with the specific heat of the body, and inversely 
with its conducting power. 

The specific heats of water, alcohol and mercury are i, 0.6 and 0.03 
Btu/lb F, respectively. After Rumford's time, Joseph Fourier (1822) 
showed that the "conducting power" of a substance, now usually called 
its thermal conductivity, can be most usefully defined as the quantity 
o heat, expressed in British thermal units, that will be transferred each 
second between opposite faces of a cube of that substance i ft on an 
edge when the temperature difference of the opposite faces is i F. The 
thermal conductivities of water, alcohol, and mercury are now known 
to be in the ratios of i.o to 0.35 to 12. Other things being equal, the 
time required to raise or lower the temperature of an object by some 
given amount is directly proportional to the specific heat and inversely 
proportional to the thermal conductivity of the substance comprising 
the object. 

The bottles were attached to the balance arms by silver wires about 2 
inches long, with hooks at the ends of them; and, in removing and 
changing the bottles, I took care not to touch the glass. I likewise avoided 
upon all occasions, and particularly in the cold room, coming near the 
balance with my breath, or touching it, or any part of the apparatus, 
with my naked hands. 

Having determined that water does not acquire or lose any weight 
upon being changed from a state of liquid to that of ice, and vice versa, 
I shall now take my final leave of a subject which has long occupied me, 
and which has cost me much pains and trouble; for I am fully convinced, 
from the results of the afore-mentioned experiments, that if heat be in 
fact a substance, or matter a fluid sui generis, as has been supposed 
which, passing from one body to another, and being accumulated, is the 
immediate cause of the phenomena we observe in heated bodies, it must 
be something so infinitely rare, even in its most condensed state, as to 
baffle all our attempts to discover its weight. And if the opinion which 


has been adopted by many of our ablest philosophers, that heat is noth- 
ing more than an intestine [internal] vibratory motion of the constituent 
parts of heated bodies, should be well founded, it is clear that the weights 
of bodies can in no wise be affected by such motion. 

It is, no doubt, upon the supposition that heat is a substance distinct 
from the heated body, and which is accumulated in it, that all the ex- 
periments have been undertaken with a view to determine the weight 
which bodies have been supposed to gain or to lose upon being heated or 
cooled; and it is toward this supposition but without, however, 
adopting it entirely, as I do not conceive it to be sufficiently proved 
that all my researches have been directed. 

The experiments with water and with ice were made in a manner 
which I take to be perfectly unexceptionable, in which no foreign cause 
whatever could affect the results of them; and since the quantity of heat 
which water is known to part with upon freezing is so considerable, if 
this loss has no effect upon its apparent weight, it may be presumed that 
we shall never be able to contrive an experiment by which we can render 
the weight of heat sensible. 

We omit the concluding paragraphs, in which Rumford explains in 
some detail why he believed his experiments with ice and water to be 
the most favorable that could be contrived for detecting the weight of 
heat. Part of his argument is similar to that given in our comments on 
page 49. He closes the paper with the remark that follows. 

I think we may safely conclude that ALL ATTEMPTS TO DISCOVER ANY 


One may question whether Rumford was justified in making a 
conclusion of such breadth and finality. For instance, A. Tilloch, in 
the Philosophical Magazine, vol. 9 (1801), p. 158, of which periodical 
he was then the editor, tried to show that Rumford's experiments, as 
well as the earlier direct attempts to weigh heat, involved a fallacy and 
were not conclusive. Tilloch's criticism was based on the fact that all 
the weighings were made in air, which, as is well known, exerts a 
buoyant effect on any object immersed in it. This vertically upward, or 
buoyant, force is, in accordance with Archimedes' principle of buoy- 
ancy, equal in magnitude to the weight of the air displaced by the 
object. When an object is weighed on a balance, both the object and 
the balancing weights are of course buoyed up by the air* However, if 
the volume of air displaced by the object differs from that displaced 
by the weights, the buoyant effects upon the two sides of the balance 
are different. Under this circumstance, the balancing weights do not 
accurately represent the true weight of the object, that is, its weight 

168 CASE 3 

in a vacuum. For instance, a bundle of feathers that weighs i Ib in a 
vacuum has an apparent weight of about 0.99 Ib in air. 

Tilloch illustrated his argument by citing the example of objects 
immersed in water. If a bit of cork is attached to a piece of metal, the 
true weight of the combination will of course be larger than that of the 
metal alone. But if this combination of metal and cork is weighed 
when immersed in water, its apparent weight will be found to be 
smaller than that of the metal alone. One can show that this will always 
be true when one object of the combination is of larger density, and 
the other is of smaller density, than the water. If the material attached 
to the immersed metal has the same density as water, the apparent 
weight of the combination will be the same as that of the metal alone. 

Now, argued Tilloch, suppose that heat actually does have weight, 
but that its density is less than that of air. Then, when heat is removed 
from an object, as in cooling or freezing it, the weight of the object in 
air would appear to increase, just as the weight of the metal in water 
would appear to increase if the cork were detached from it. This was 
precisely what Fordyce had observed : the weight of his liquid appeared 
to increase when heat was removed from it. It should be noted that 
Tilloch had here provided a way to explain an increase in the weight 
of an object upon losing heat without having to resort to the ad hoc 
assumption that heat has negative weight. However, his argument is 
not valid unless it is assumed that the volume of air displaced by an 
object containing heat is larger than the volume displaced after some 
of the heat has been removed. 

Rumford, in his final and very accurate experiments, observed no 
change in the weight of a liquid when heat was subtracted from or 
added to it. But Tilloch could also explain this result, simply by 
assuming that the density of heat was equal to, and not smaller than, 
the density of air. 

Tilloch's ingenious argument provides a good illustration of how 
difficult it is to devise a simple type of experiment that will settle a 
question, such as that about the weight of heat, in a conclusive and 
unambiguous manner. However, his argument involved assumptions 
that Rumford could have questioned, in view of the procedure that he 
had used in his final weighings. Moreover, Tilloch's essential objection 
could have been removed by repeating the weighings in a vacuum, 
although such experiments would not have been easy to carry out. 

Even if Rumford had made the weighings in a vacuum, the calorists 
could still have argued either that heat was "weightless," and yet had 
all the other properties characteristic of a material substance, or else 
that it was too "subtle" for its weight to be detected. This raises the 
important question whether it is useful and meaningful to assume the 


existence of any entity or property, once it has become clear that there 
is no way whatever to detect it. 

Joseph Black had been of the opinion that heat did not have weight, 
and he had considered this to be one of the chief objections to the caloric 
theory (p. 153). But to many other scientists and philosophers of the 
eighteenth century, this would not have been regarded as a serious 
objection. It was currently believed that there was a small class of 
"imponderable substances," which at the time included light, electricity 
and magnetism, that, unlike ordinary matter, were not subject to 
gravitational attraction, at least to any observable extent. Yet, on the 
assumption that these "substances" exhibited certain other familiar 
properties of ordinary matter, the various phenomena known at the 
time could be connected fairly satisfactorily, and new phenomena often 
could be successfully predicted. Thus, the question whether heat had 
weight was deemed less critical in trying to distinguish between the 
caloric and mode-of-motion theories than was, for example, the ques- 
tion of the validity of the principle of conservation of heat, which was 
the most basic postulate of the caloric theory. Rumford was able to 
throw some light on this latter question in other experiments (Sec. 4) 
carried out as part of his program of attack on the caloric theory. 

Although Rumford's experiments on the weight of heat may not 
have been completely conclusive, they undoubtedly were the best of all 
the experiments carried out on this subject. Indeed, the present paper 
has been characterized as describing a magnificent experimental tech- 
nique and a classic example of what scientific investigation is at its 


The most celebrated experiments carried out by Count Rum- 
ford were those concerned with the heat produced during the boring 
of cannon. The caloric theory had been found especially helpful in 
explaining and predicting phenomena in which heat passes from one 
body to another by conduction as when liquids are mixed or when 
a substance placed over a fire is warmed, melted, or vaporized. For such 
phenomena, it is worth noting, one can safely assume that there is no 
creation or destruction of heat during its passage from one object to 
another, or from a fire to an object. 

But whence comes the heat when an object is warmed, not by fire, 
but by rubbing or hammering it? The supporters of the caloric theory 
believed that they could also answer this question satisfactorily, and 
still retain their principle that heat can be neither created nor destroyed. 

170 CASE 3 

But there were other Investigators who thought that the mode-of- 
motion theory offered a better explanation. As early as 1620, Francis 
Bacon, in the Second Book of his Novitm Organum, expressed the idea 
that new heat comes into existence when an object is rubbed or ham- 
mered, and from this he concluded that "heat itself, its essence and 
quiddity, is motion and nothing else." The same view was expressed 
later in the seventeenth century by Boyle and by Hooke, and also by 
many philosophers of the period. Early in the eighteenth century, the 
philosopher John Locke, in his Elements of Natural Philosophy (1722), 
supported the idea that heat is a kind of motion by citing various ways 
in which it is produced; for example, "the axle-trees of carts and 
coaches are often made hot, and sometimes to a degree that it sets them 
on fire, by the rubbing of the naves of the wheels upon them." "On 
the other side," he said, "the utmost degree of cold is the cessation of 
that motion of the insensible particles." 

Rumford carried out his cannon-boring experiments at the military 
arsenal in Munich, of which he was in charge. He reported them in a 
paper entitled "An Inquiry Concerning the Source of Heat which is 
Excited by Friction," which he read at a meeting of the Royal Society 
In January 1798 and later published in the Philosophical Transactions,, 
vol. 88 (1798), p. 80. The edited and annotated version that follows is 
based on the paper as it was reprinted in The Complete Worlds of 
Count Rumford (American Academy of Arts and Sciences, 1870), 
vol. I, pp. 471-493- 



Benjamin Thompson (Count Rumford) 

It frequently happens that in the ordinary affairs and occupations of 
life, opportunities present themselves of contemplating some of the most 
curious operations of Nature; and very Interesting philosophical experi- 
ments might often be made, almost without trouble or expense, by means 
of machinery contrived for the mere mechanical purposes of the arts and 

I have frequently had occasion to make this observation; and am per- 
suaded that a habit of keeping the eyes open to everything that is going 
on In the ordinary course of the business of life has oftener led as it 
were by accident, or in the playful excursions of the imagination, put into 
action by contemplating the most common appearances to useful 
doubts and sensible schemes for investigation and improvement than all 


the more intense meditations of philosophers in the hours expressly set 
apart for study. 

It was by accident that I was led to make the experiments of which I 
am about to give an account; and, though they are not perhaps of suffi- 
cient importance to merit so formal an introduction, I cannot help flat- 
tering myself that they will be thought curious in several respects, and 
worthy of the honor of being made known to the Royal Society. 

Being engaged lately in superintending the boring of cannon in the 
workshops of the military arsenal at Munich, I was struck with the very 
considerable degree of heat [temperature] that a brass gun acquires in 
a short time in being bored, and with the still higher temperature (much 
higher than that of boiling water, as I found by experiment) of the 
metallic chips separated from it by the borer. 

The more I meditated on these phenomena, the more they appeared 
to me to be curious and interesting. A thorough investigation of them 
seemed even to bid fair to give a farther insight into the hidden nature 
of heat; and to enable us to form some reasonable conjectures respecting 
the existence, or nonexistence, of an igneous fluid a subject on which 
the opinions of philosophers have m all ages been much divided. 

As Rumford says, he began these experiments "by accident," that is, 
as the result of what he observed while engaged in his regular work 
as superintendent of the arsenal at Munich. One might ask whether the 
making of such experiments would be likely to have occurred acciden- 
tally to a person unfamiliar with the currently known facts, experi- 
mental methods, and theories about heat or to a person who lacked 
Rumford's "habit of keeping the eyes open to everything that is going 
on in the ordinary course of the business of life." 

There was nothing extraordinary about his mere observation that 
heat is produced during the boring of a gun. Since the earliest times it 
had been known that heat could be developed by friction as when 
primitive people made a fire by rapidly rotating a pointed stick inserted 
in a hole drilled in dry wood. Rumford's feats here were that he 
noticed the very high temperature quickly acquired by the gun during 
the boring and saw how further study of this phenomenon might 
throw new light on the "hidden nature of heat." 

By "igneous fluid" Rumford means the "subtle elastic fluid" which, 
according to the caloric theory, constituted heat. In the literature of his 
period, the terms "igneous fluid," "heat fluid," "matter of heat," 
"caloric," "calor," and "heat" were used more or less interchangeably. 
The term "caloric" actually was not introduced until comparatively 
late in the history of the conception of heat as a substance, having been 
coined in 1787 by Lavoisier and other French scientists during a revision 
of chemical terminology which they carried out at that time. The term 

172 CASE 3 

"calorimeter," which is still used today to refer to any apparatus for 
measuring quantities of heat, was coined by Lavoisier in 1789. 

In order that the Society may have clear and distinct ideas of the specu- 
lations and reasonings to which these appearances gave rise in my mind, 
and also of the specific objects of philosophical investigation they sug- 
gested to me, I must beg leave to state them at some length, and in 
such manner as I shall think best suited to answer this purpose. 

From whence comes the heat actually produced in the mechanical 
operation above mentioned? 

Is it furnished by the metallic chips which are separated by the borer 
from the solid mass of metal? If this were the case, then, according to 
the modern doctrines of latent heat and of caloric, the specific heat of the 
parts of the metal, so reduced to chips, ought not only to be changed, but 
the change undergone by them should be sufficiently large to account for 
all the heat produced. 

But no such change had taken place; for I found, upon taking equal 
weights of these chips and of thin slips separated from the same block of 
metal by means of a fine saw, and putting them at the same temperature 
(that of boiling water) into equal weights of cold water initially at the 
temperature of 59 1 /2F J the portion of water into which the chips were 
put was not, to all appearance, heated either less or more than the other 
portion in which the slips of metal were put. This experiment being re- 
peated several times, the results were always so nearly the same that I 
could not determine whether any, or what, change had been produced in 
the metal, in regard to its specific heat, by being reduced to chips by the 

In boring a cannon, or whenever one solid object is rubbed against 
another, the rubbing surfaces are abraded, that is, rubbed or cut into 
dust or chips. Might these chips possibly be the source of the large 
quantity of heat produced during the boring? If so, asserts Rumford, 
it follows from the "modern" caloric theory that the specific heat of the 
chips should be different from that of the metal in bulk. Suppose it 
were found that the specific heat of the chips was smaller than that of 
the metal in bulk. Then this could be interpreted to mean that the 
attractive force was smaller between the chips and caloric than between 
the bulk metal and caloric, and hence that caloric would be set free 
during the abrasion. Indeed, this was one way in which the calorists 
had tried to explain heat produced by friction; yet no one prior to 
Rumford seemingly had made experiments to determine whether there 
was any difference in the specific heats of the abraded and the bulk 

To find the specific heat of the cannon metal, Rumford here has 
made use of the technique in calorimetry known as the method of 


mixtures (Sec. 2). He took slices of the bulk metal, determined their 
weight / 6 and initial temperature % and then put them in a known 
weight w w of water initially at a known temperature t^. Let t be the 
observed, equilibrium temperature of the mixture of metal and water. 
Then the heat lost by the bulk metal is given by the expression 
*& ^5 (*6 ~ *)> where s b is the unknown specific heat of the metal; and 
the heat gained by the water is given by s w w w (t t w }, where s w Is 
the specific heat of water. Assuming the experiment to have been so 
devised that the heat lost by the metal was equal to the heat gained by 
the water, we can write the equation 

^ w b (t b - t) = s lc w w (t - t w ). (5) 

Rumford next repeated this whole method-of-mixtures experiment, 
this time substituting chips bored from the same block of cannon metal 
for the bulkier slices, but keeping the weights and the initial tempera- 
tures the same as before; and he observed the temperature of the 
mixture of chips and water again to be /, the same as in the preceding 
experiment. If s e denotes the specific heat of the metal chips, the equa- 
tion for this second experiment is 

*c w b (h - t) = s w w w (t - t w ). (6) 

By comparing Eqs. (5) and (6) we can conclude, as did Rumford, 
that the specific heats s b and s c are equal. 

Suppose it had been found that the specific heat of the chips was not 
equal to that of the metal in bulk. Then, as Rumford points out, the 
next question for investigation would have been whether this change in 
specific heat upon abrasion was "sufficiently large to account for all the 
heat produced." Often an explanation or a hypothesis will turn out to 
be admissible qualitatively ', but not quantitatively. As a simple example, 
a very early hypothesis as to the source of solar energy was that the sun 
is a mass of fuel, such as coal, which is burning and thus emitting 
energy. This hypothesis passed the qualitative test in that it is true that 
a burning fuel emits energy. But when, later, our knowledge of fuels, 
of the size and distance of the sun, and of the energy given off by it 
was sufficiently complete to make even rough calculations possible, it 
became clear that the sun, if it were simply a ball of burning fuel, would 
have been completely consumed long ago. The hypothesis met the 
qualitative but not the quantitative test. 

As these experiments [on the specific heats of the abraded and bulk 
metal] are important, it may perhaps be agreeable to the Society to be 
made acquainted with them in their details. One of them is as follows: 

To 4590 grains [0.66 Ib] of water, at the temperature of 59% F (in* 

174 CASE 3 

eluded in this weight was an allowance, reckoned in terms of water, for 
the heat capacity of the containing tin vessel), were added 1016% grains 
[0.16 Ib] of cannon metal in thin slips, these being at 2ioF, the temper- 
ature of boiling water at Munich. When they had remained together i 
minute, and had been well stirred about by means of a small rod of light 
wood, the temperature of the mixture was found to be 63 R From this 
experiment the specific heat of the metal, calculated according to the rule 
given by Dr. Crawford, turns out to be o.noo [Btu/lb F], that of water 
being i.oooo [Btu/lb F]. 

An experiment was afterwards made with the metallic chips as fol- 
lows. To the same weight of water as was used in the afore-mentioned 
experiment, at the same temperature (59%F) and in the same cylin- 
drical tin vessel, were now put ioi6 l /s grains of metallic chips bored out 
of the same gun from which the slips used in the foregoing experiment 
were taken, and at the same temperature (210 F). The temperature of 
the mixture at the end of i minute was 63 F, as before. Consequently, 
the specific heat of these metallic chips is o.noo [Btu/lb F], Each of 
the foregoing experiments was repeated three times, and always with 
nearly the same results. 

The "rule given by Dr. Crawford," which Rumford says he used in 
calculating the specific heats, is essentially the one for the method of 
mixtures described in our note on page 173; that is, one writes an equa- 
tion which contains in one member all the quantities representing heat 
gained by the warming bodies and, in the other member, all the quanti- 
ties representing heat lost by the cooling bodies. In the present experi- 
ment, the water and its containing vessel are the warming bodies, and 
the cannon metal is the cooling body. Rumford probably found this 
rule in Crawford's Experiments and Observations on Animal Heat, etc. 
(ed. i, 1779; ed. 2, 1788). Although most of the features of the method 
of mixtures were developed earlier by Black and Irvine (Sec. 2), at 
least one improvement was made by Crawford; he suggested that the 
transfer of heat to and from the surrounding air can be reduced by so 
choosing the values of the initial temperatures of the warming and cool- 
ing bodies that the temperature of the mixture will be approximately 
the same as that of the surrounding air. 

Strictly speaking, Rumford's demonstration that the chips and bulk 
metal have the same specific heat at the same temperature did not con- 
stitute a complete refutation of the calorists' explanation of how heat 
was developed by friction. To show that the two specific heats are equal 
may have been necessary, but it was not sufficient. For a more conclusive 
test, it was still necessary to show that equal weights of the chips and 
bulk metal always contained equal quantities of heat when at the same 
temperature. The calorists could have said that, even though the chips 


and bulk metal had the same specific heats at the same temperature, yet 
the bulk metal contained more latent heat than the chips, the difference 
having been evolved during abrasion. A possible test of this contention 
would have been to measure the quantities of heat needed to melt equal 
weights of chips and of bulk metal. If these quantities of heat were 
found equal, and if it were granted that the resulting liquids were in 
all respects exactly the same, then one could conclude that equal weights 
of the chips and bulk metal contained equal quantities of heat at the 
same temperature. However, we shall see that Rumford did not bother 
to carry out such an experiment; a possible reason for this is suggested 
in our note on page 188. 

One supporter of the caloric theory asserted, in 1830, that none of the 
afore-mentioned experiments on specific heats had any significance in 
determining whether or not the heat evolved during boring came from 
the metal chips. He contended that this heat could have come, not from 
the chips, but from the layer of bulk metal in contact with the borer. 
The large force to which this layer was subjected would tend to com- 
press it and increase its density; and it had long been known that when 
any piece of metal is compressed, as by hammering it, heat is evolved. 
This heat, the calorists said, was squeezed out of the metal as a result 
of the compression. Thus, in the boring of the cannon, successive fresh 
layers of cannon metal were exposed to compression as the result of the 
abrasion, and hence each layer in succession would release a certain 
quantity of heat. If any changes in density or specific heat occurred, it 
would therefore be confined to the surface layer of the bulk metal, and 
this Rumford did not test. 

The passages that follow will be easier to interpret if it is remembered 
that Rumford and some other scientists of his period used the expression 
"latent heat" to refer, not solely to heats of fusion and vaporization, as 
Black had done (Sec. 2), but also to heat which the calorists assumed 
was stored in an inactive form in any substance and released upon rub- 
bing or hammering it. 

It is evident that the heat produced could not possibly have been 
furnished at the expense of the latent heat of the metallic chips. But, not 
being willing to rest satisfied with these trials, however conclusive they 
appeared to me to be, I had recourse to the following still more decisive 

Taking a cannon (a brass six-pounder), cast solid, and rough as It 
came from the foundry (see Fig, i in Plate II), and fixing it horizontally 
in the machine used for boring, and at the same time finishing the outside 
of the cannon by turning (see Fig. 2), I caused its extremity to be cut 
off and the metal in that part to be turned down to form a solid cylinder, 
7% inches in diameter and 9^0 inches long. This cylinder, when fin- 

PLATE II. RumforcTs diagrams of his apparatus. 


ished, remained joined to the rest of the metal (that which, properly 
speaking, constituted the cannon) by a small cylindrical neck only 2% 
inches in diameter and 3%o inches long. 

This short cylinder, which was supported in its horizontal position 
and could be turned round its axis by means of the neck that united it 
to the cannon, was now bored with the horizontal borer used in boring 
cannon; but its bore, which was 3.7 inches in diameter, instead of being 
continued through its whole length (9.8 inches) was only 7.2 inches in 
length; so that a solid bottom was left to this hollow cylinder, which 
bottom was 2.6 inches in thickness. This cavity is represented by dotted 
lines in Fig. 2 and also in Fig. 3, where the cylinder is represented on an 
enlarged scale. 

This cylinder was designed for the express purpose of generating heat 
by friction, by forcing a blunt borer against the solid bottom of the 
cylinder at the same time that the latter was turned round its axis by 
the force of horses. In order that the temperature of the cylinder might 
from time to time be measured, a small round hole (see de. Fig. 3), only 
0.37 inch in diameter and 4.2 inches in depth, was made in it for the 
purpose of introducing a small cylindrical mercurial thermometer. This 
hole was on one side, in a direction perpendicular to the axis of the 
cylinder, and ended in the middle of the solid bottom. 

The volume of the hollow cylinder, exclusive of the cylindrical neck 
by which it remained united to the cannon, was 385% cubic inches, 
English measure, and it weighed 113.13 Ib avoirdupois; this I found on 
weighing it at the end of the course of experiments, and after it had 
been separated from the cannon. 

Note. For fear I should be suspected of prodigality in the prosecution 
of my philosophical researches, I think it necessary to inform the Society 
that the cannon I made use of in this experiment was not sacrificed to 
it. The short hollow cylinder which was formed at the end of it was 
turned out of a cylindrical mass of metal, about 2 feet in length, project- 
ing beyond the muzzle of the gun, called in the German language the 
verlorner J(ppj (the head of the cannon to be thrown away) and which 
is represented in Fig. i. This original projection, which is cut off before 
the gun is bored, is always cast with it, in order that, by means of its 
weight on the metal in the lower part of the mould during the time it is 
cooling, the gun may be the more compact in the neighborhood of the 
muzzle, where, without this precaution, the metal would be apt to be 
porous, or full of honeycombs. 

The reader who is acquainted with the general history of this period 
may be able to suggest reasons why Rumford seems to feel it necessary 
to explain that the cannon was not destroyed in the course of these 
philosophical researches. By "philosophical research" he means what we, 
today, often call "pure research," as distinguished from research in en- 
gineering and technology. 

178 CASE 3 

Experiment No. I 

This experiment was made in order to ascertain how much heat was 
actually generated by friction when the blunt steel borer was so forcibly 
shoved (by means of a strong screw) against the bottom of the bore of 
the cylinder that the pressing force on it was equivalent to the weight 
of about 10,000 Ib avoirdupois and the cylinder was being turned round 
on its axis (by the force of horses) at the rate of about 32 times in a 
minute. This machinery, as it was put together for the experiment, is 
represented by Fig. 2. Here w is a strong horizontal iron bar, connected 
with proper machinery carried round by horses, by means of which the 
cannon was made to turn round its axis. 

To prevent, as far as possible, the loss of any part of the heat that was 
generated in the experiment, the cylinder was well covered up with a 
fit coating of thick and warm flannel, which was carefully wrapped 
round it, and defended it on every side from the cold air of the atmos- 
phere. This covering is not shown in Fig. 2. 

I ought to mention that the borer was a flat piece of hardened steel, 
0.63 of an inch thick, 4 inches long, and nearly as wide as the cavity of 
the bore of the cylinder, namely, 3% inches. Its corners were rounded 
off at its end, so as to make it fit the hollow bottom of the bore; and it 
was firmly fastened to the iron bar m which kept it in its place. The area 
of the surface by which its end was in contact with the bottom of the 
bore of the cylinder was nearly 2% square inches. This borer, which is 
distinguished by the letter n, is represented in most of the figures. 

At the beginning of the experiment, the temperature of the air in the 
shade, as also that of the cylinder, was 60 F. At the end of 30 minutes, 
when the cylinder had made 960 revolutions about its axis, the horses 
being stopped, a cylindrical mercurial thermometer, whose bulb was 
3 %oo an i ncri * n diameter and 3% inches in length, was introduced 
into the hole de in the side of the cylinder; the mercury rose almost in- 
stantly to i30F. 

The heat could not be supposed to be quite equally distributed in 
every part of the cylinder, yet, as the length of the bulb of the thermom- 
eter was such that it extended from the axis of the cylinder to near its 
surface, the temperature indicated by it could not be very different from 
the mean temperature of the cylinder; and it was on this account that a 
thermometer of that particular form was chosen for this experiment. 

To see how fast the heat escaped from the cylinder (in order to be able 
to make a probable conjecture respecting the quantity given off by it 
during the time the heat generated by the friction was accumulating), 
the machinery standing still, I suffered the thermometer to remain in its 
place nearly three quarters of an hour, observing and noting down, at 
small intervals of time, the temperature indicated by it. [See Table i.] 

As Rumford states, the boring in experiment No. i was carried on for 
30 min, during which time the temperature of the cylinder rose from 


60 to 130 R The cylinder was wrapped in flannel, but as the cooling 
data in Table i show, some o the heat evolved during the boring es- 
caped to the surrounding objects and atmosphere. From these cooling 
data, Rumford could have estimated how much above i30F the final 
temperature o the cylinder would have been if it had been perfectly 
insulated from the surroundings. However, we see from Table i that, 
at the highest temperatures, the time-rate of cooling never exceeded one 
degree per minute, and at temperatures near that of the air (60 F) the 
rate was much smaller. So he does not bother to complete the calcula- 
tions or to comment further on these cooling data. 

[TABLE i. Cooling data.] 

Total time, in minutes, Temperature, in degrees 

since machinery was Fahrenheit, as shown by 

stopped the thermometer 

_ . _ 

4 126 

5 125 
7 123 

12 120 

14 119 

16 118 

20 Il6 

24 115 

28 114 

3* "3 

34 112 

37/2 in 

41 110 

Having taken away the borer, I now removed the metallic dust, or, 
rather, scaly matter, which had been detached from the bottom of the 
cylinder by the blunt steel borer. I carefully weighed this dust and found 
its weight to be 837 grains. 

Is it possible that the very considerable quantity of heat produced in 
this experiment (a quantity which actually raised the temperature of 
above 113 Ib of gun metal at least 70 Fahrenheit degrees, and which, of 
course, would have been capable of melting 6 l / 2 Ib of ice) could have 
been furnished by so inconsiderable a quantity of metallic dust? And 
this merely in consequence of a change of its specific heat? 

As the weight of this dust (837 grains) amounted to no more than 
i /948th part of that of the cylinder, the dust would have had to give up 
a quantity of heat equal to that which it would lose in cooling through 
948 Fahrenheit degrees to have been able to raise the temperature of the 

180 CASE 3 

cylinder i; and consequently it would have had to give up a quantity 
corresponding to a cooling through 66,360 Fahrenheit degrees to have 
produced the effects that were actually observed in the experiment! 

Rumford had previously found the specific heat of the cannon metal 
to be o.n Btu/lb F. The cylinder weighed 113 Ib, and its temperature 
during boring increased at least (130-60) F, or 70 Fahrenheit degrees. 
So the quantity of heat entering the cylinder during boring was at least 
(o.n Btu/lb F) X 113 Ib X 70F, or 870 Btu. 

That this really is a considerable quantity of heat is strikingly illus- 
trated by Rumford's remark that it is sufficient to melt 6.5 Ib of ice. 
Using the modem value of the heat of fusion of ice, namely, 144 Btu/lb, 
we see that the weight of ice that would be melted by 870 Btu of heat 
is 870 Btu/(i44 Btu/lb), or about 6.0 Ib. Rumford, in arriving at the 
larger figure of 6.5 Ib for the weight of ice that would be melted, prob- 
ably took into account the fact that, if a correction for cooling had been 
made, the value for the final temperature of the cylinder would have 
exceeded I30F. Moreover, in his day the heat of fusion of ice was often 
taken to be Black's value of 141 Btu/lb, instead of the more correct 
modern value of 144 Btu/lb. 

In saying that the metallic dust would have had to cool through 
66,360 Fahrenheit degrees to have produced the effects observed, Rum- 
ford is not implying that the dust is to be thought of as actually having 
undergone this drop in temperature. The British thermal unit had not 
yet come into use and so Rumford, like Black (Sec. 2), had to express 
quantity of heat in some other way for instance, in terms of the tem- 
perature change that it would produce in some specified substance. If 
the British thermal unit had been available to him, he very likely would 
have stated his argument somewhat as follows. The quantity of heat 
evolved in 30 min was at least 870 Btu. To gain an idea of the magni- 
tude of this quantity, notice that it would be sufficient to melt more 
than 6 Ib of ice or, as another illustration, sufficient to produce a tem- 
perature change of 66,360 Fahrenheit degrees in 837 grains of metallic 

This temperature change can be computed as follows. The quantity 
of heat H m absorbed by the bulk metal was equal to sw X 70 F, where 
s and w are the specific heat and weight of this metal, respectively. The 
quantity of heat H d needed to produce a temperature change A/ in the 
dust is given by s(w/g$)te, on the assumption that the specific heat 
of the dust is practically equal to that of the bulk metal If H m =H d , then 

sw X 70F = s (//948)A*, 

At = 948 X 7oF = 66,360 F. 


Incidentally, there is no justification for retaining five significant fig- 
ures in this result. Rumford was not always consistent in his use of 
significant figures. 

If Rumford could have used modern units, he might have continued 
his argument in this fashion. If the release of 870 Btu of heat actually 
had been due to a change in the specific heat of the metal upon abrasion, 
this would mean that "so inconsiderable a quantity" of metal as 837 
grains (0.1197 Ib) must have released 870 Btu upon being reduced to 
dust. In other words, the release of heat would have been 870 6111/0.1197 
Ib, or about 7300 Btu per pound of metal, "and this merely in conse- 
quence of a change in its specific heat." This could have well seemed 
"improbable" to Rumford, in view of his knowledge of the quantities 
of heat that are released under other somewhat comparable circum- 
stances. For instance, compare this figure of 7300 Btu per pound with 
the 144 Btu of heat released by a pound of water when it freezes, or 
even with the 970 Btu released by a pound of steam when it liquefies. 

But without insisting on the improbability of this supposition, we have 
only to recollect that, from the results of actual and decisive experiments 
made for the express purpose of ascertaining that fact, the specific heat 
of the metal of which great guns are cast is not sensibly changed by being 
reduced to the form of metallic chips in the operation of boring cannon; 
and there does not seem to be any reason to think that it can be much 
changed, if it be changed at all, in being reduced to much smaller pieces 
by means of a borer that is less sharp. 

If the heat, or any considerable part of it, were produced in conse- 
quence of a change in the specific heat of a part of the metal of the 
cylinder, as such change could only be superficial, the cylinder would by 
degrees be exhausted; or the quantities of heat produced in any given 
short interval of time would be found to diminish gradually in successive 
experiments. To find out if this really happened or not, I repeated the 
last-mentioned experiment several times with the utmost care; but I did 
not discover the smallest sign of exhaustion in the metal, notwithstanding 
the large quantities of heat actually given off. 

Finding so much reason to conclude that the heat generated or ex- 
cited, as I would rather choose to express it in these experiments was 
not furnished at the expense of the latent heat or combined caloric of the 
metal, I pushed my inquiries a step farther and endeavored to find out 
whether or not the air contributed anything in the generation of it. 

Experiment No. 2 

As the bore of the cylinder was cylindrical, and as the iron bar w, to 
the end of which the blunt steel borer was fixed, was square, the air had 
free access to the inside of the bore, and even to the bottom of it, where 
the friction took place by which the heat was excited. 

182 CASE 3 

As neither the metallic chips produced in the ordinary course of the 
operation of boring brass cannon, nor the finer scaly particles produced 
in the last-mentioned experiments by the friction of the blunt borer, 
showed any signs of calcination [oxidation], I did not see how the air 
could possibly have been the cause of the heat that was produced; but, 
in an investigation of this kind, I thought that no pains should be spared 
to clear away the rubbish, and leave the subject as naked and open to 
inspection as possible. 

In order, by one decisive experiment, to determine whether or not the 
air of the atmosphere had any part in the generation of the heat, I con- 
trived to repeat the experiment under circumstances in which // was evi- 
dently impossible for it to produce any effect whatever. A piston was 
exactly fitted to the mouth of the bore of the cylinder, and through the 
middle of this piston the square iron bar m, to the end of which the blunt 
steel borer was fixed, passed in a square hole made perfectly airtight. 
Thus the access of the external air to the inside of the bore of the cylinder 
was effectually prevented. (In Fig. 3, this piston p is seen in its place; it 
is likewise shown in Figs. 7 and 8.) 

I did not find, however, by this experiment that the exclusion of the 
air diminished, in the smallest degree, the quantity of heat excited by 
the friction. 

There still remained one doubt, which, though it appeared to rne to be 
so slight as hardly to deserve any attention, I was however desirous to 
remove. The piston /?, in order that it might be airtight, was fitted into 
the mouth of the bore of the cylinder with so much nicety, by means of 
collars of leather, and pressed against it with so much force, that, not- 
withstanding its being oiled, it occasioned a considerable amount of 
friction when the hollow cylinder was turned round its axis. Was not the 
heat, or at least some part of it, occasioned by this friction of the piston? 
And, as the external air had free access to the extremity of the bore, where 
it came in contact with the piston, is it not possible that this air may 
have had some share in the generation of the heat produced ? 

Experiment No. 3 

A quadrangular oblong deal box (Fig. 4), watertight, n l / 2 English 
inches long, 9^0 inches wide, and 9% inches deep (measured in the 
clear), was provided with holes or slits in the middle of each of its ends, 
just large enough to receive, the one the square iron rod m to the end of 
which the blunt steel borer was fastened, the other the small cylindrical 
neck which joined the hollow cylinder to the cannon. This box could be 
closed above by a wooden cover or lid moving on hinges. By means of 
the two vertical openings or slits in its two ends (the upper parts of 
which openings could be closed by means of narrow pieces of wood 
sliding in vertical grooves), the box (ghi\, Fig. 3) was fixed to the 
machinery in such a manner that its bottom i\ was horizontal and its 
axis coincided with the axis of the hollow metallic cylinder. It is evident 


from the description that the hollow metallic cylinder occupied the 
middle of the box, without touching it on either side (see Fig. 3); and 
that, on pouring water into the box, and filling it to the brim, the 
cylinder was completely covered and surrounded on every side by that 
fluid. And further, as the box was held fast by the strong square iron 
rod m which passed through the square hole in the center of its left-hand 
end (Fig. 4), while the round or cylindrical neck, which joined the 
hollow cylinder to the end of the cannon, could turn round freely on its 
axis in the round hole in the center of the right-hand end, it is evident 
that the machinery could be put in motion without the least danger of 
forcing the box out of its place, throwing the water out of it, or derang- 
ing any part of the apparatus. 

The hollow cylinder having been previously cleaned out, and the 
inside of its bore wiped with a clean towel till it was quite dry, the 
square iron bar m, with the blunt steel borer n fixed to the end of it, was 
put into place; the mouth of the bore of the cylinder was closed at the 
same time by means of the circular piston p through the center of which 
the iron bar m passed. The box was now put in place, and the joinings 
of the iron rod and of the neck of the cylinder with the two ends of the 
box were made watertight by means of collars of oiled leather. The box 
was then filled with cold water of temperature 60 F, and the machinery 
was put in motion. 

The result of this beautiful experiment was very striking, and the 
pleasure it afforded me amply repaid me for all the trouble I had had in 
contriving and arranging the complicated machinery used in making it. 

The cylinder, revolving at the rate of about 32 times in a minute, had 
been in motion but a short time when I perceived, by putting my hand 
into the water and touching the outside of the cylinder, that heat was 
being generated; and it was not long before the water which surrounded 
the cylinder began to be sensibly warm. 

At the end of i hour I found, by plunging a thermometer into the 
water in the box (the weight of this water was 18.77 ^ avoirdupois, or 
2% wine gallons), that its temperature had been raised no less than 47 
degrees, being now io7F. When 30 minutes more had elapsed, or i% 
hours after the machinery had been put in motion, the temperature of 
the water in the box was i42F. At the end of 2 hours, reckoning from 
the beginning of the experiment, the temperature of the water was found 
to be i78F. At 2 hours and 20 minutes it was 200 F. At 2% hours it 


It would be difficult to describe the surprise and astonishment expressed 
in the countenances of the bystanders on seeing so large a quantity of 
cold water heated, and actually made to boil, without any fire. Though 
there was, in fact, nothing that could justly be considered as surprising 
in this event, yet I acknowledged fairly that it afforded me a degree of 
childish pleasure, which, were I ambitious of the reputation of a grave 
philosopher^ I ought most certainly rather to hide than to discover. 

184 CASE 3 

The quantity of heat excited and accumulated in this experiment was 
very considerable; for, not only the water in the box, but also the box 
itself (which weighed 15% Ib), and the hollow metallic cylinder, and 
that part of the iron bar which, being situated within the cavity of the 
box, was immersed in the water, were heated through 150 degrees 
that is, from 60 F (which was the temperature of the water and of the 
machinery at the beginning of the experiment) to 2ioF, the tempera- 
ture of boiling water at Munich. 

The total quantity of heat generated may be estimated with some 
considerable degree of precision as follows. 

We here replace Rumford's description o his calculation by a some- 
what more concise statement utilizing modern thermal units. 

Employing the formula H = swLt, which is our Eq. (4), one finds 
that the quantities of heat needed to raise the temperature of the various 
parts of the apparatus from 60 to 2ioF were: 

(i) for 1 8% Ib of water in the wooden box, 

H x = 1.0 - x 18% Ib X (210 - 60) F = 2810 Btu; 
Ib r 

(2) for 113 Ib of gun metal, of specific heat o.n Btu/lb F, compris- 
ing the hollow cylinder, 

H 2 = o.ii-x 113 Ib X (210 - 60) F = 1870 Btu; 

Ib r 

(3) for 36.75 in. 3 of iron, comprising that part of the iron bar m 
that entered the box, 

J/ 3 (as reckoned by Rumford) = 182 Btu. 

Rumford does not say how he arrived at this value of 182 Btu, but one 
can easily show that it is the quantity of heat that would be needed to 
produce a temperature rise of 150 Fahrenheit degrees in the bar m if the 
specific heat and density of the iron comprising it are taken to be 
0.115 Btu/lb F and 496 lb/ft 3 , respectively; these are approximately 
equal to the modern values for these two quantities. 

The total quantity of heat produced by friction (not taking into 
account the heat absorbed by the wooden box and that lost to the 
atmosphere during the experiment) was therefore 

H = H 1 + H^ + H Z = (2810 + 1870 + 182) Btu = 4900 Btu. 

This final value has been rounded off to two significant figures, thus 
indicating the degree of accuracy that appears to be warranted by the 


From the knowledge of the quantity of heat actually produced in the 
foregoing experiment, and of the time in which it was generated (150 
minutes), we are able to ascertain how fast it was produced and to de- 
termine how much fuel would have to be consumed in order to produce, 
in burning equably, the same quantity of heat in the same time. . . . 

The next three paragraphs are omitted. In them Rumford cites an 
experiment of Dr. Crawford's, the results of which indicate that 2.1 
Btu of heat are generated in the combustion of i grain (1/7000 Ib) of 
candle wax. Recalling that the heat generated by friction in experiment 
No. 3 was computed to be 4900 Btu, Rumford shows that 4900/2.1, or 
2300 grains, of candle wax would have to be burned to produce this 
quantity of heat. 

This attempt of Rumford's to compare the heat evolved by burning 
candles with that evolved by friction is reminiscent of experiments 
carried out several years earlier by Lavoisier and Laplace, in which they 
noted that the heat evolved by burning candles was approximately 
equal to the animal heat evolved by a guinea pig after eating food con- 
taining the same weights of carbon and hydrogen. The significance of 
such experiments is that they represent attempts to find quantitative 
relations between phenomena that later were to be more clearly recog- 
nized as representing conversions of energy from one form to another 
chemical energy into heat, mechanical energy into heat, and so on. 
The idea of correlating these phenomena was in the air. 

Now I found, by an experiment made on purpose to finish these 
computations, that when a good wax candle, of a moderate size, % inch 
in diameter, burns with a clear flame, just 49 grains of wax are consumed 
in 30 minutes. Hence it appears that 245 grains of wax would be con- 
sumed by such a candle in 150 minutes; and that to burn the 2300 grains 
necessary to produce the quantity of heat actually obtained by friction 
in the experiment in question, and in the given time (150 minutes), nine 
candles, burning at once, would not be sufficient; for 9 multiplied by 245 
(the number of grains consumed by each candle in 150 minutes) amounts 
to no more than 2205 grains; whereas the weight of wax necessary to be 
burnt, in order to produce the given quantity of heat, was found to be 
2300 grains. 

From the result of these computations it appears that the quantity of 
heat produced equably, or in a continuous stream (if I may use that 
expression), by the friction of the blunt steel borer against the bottom of 
the hollow metallic cylinder, in the experiment under consideration, was 
larger than that produced equably in the combustion of nine wax candles, 
each % of an inch in diameter, all burning at the same time with clear 
bright flames. 

As the machinery used in this experiment could easily be driven by 

186 CASE 3 

the force of one horse (though, to render the work lighter, two horses 
actually were employed), these computations show further how large a 
quantity of heat might be produced, by proper mechanical contrivance, 
merely by the strength of a horse, without either fire, light, combustion, 
or chemical decomposition; and, in a case of necessity, the heat thus 
produced might be used in cooking victuals. 

But no circumstances can be imagined in which this method of pro- 
curing heat would be advantageous; for more heat might be obtained 
by using the fodder necessary for the support of a horse as fuel. . . . 

In experiment No. i, which lasted only half an hour, the quantity of 
heat generated was found to be equal to that which would be required 
to heat 5 Ib of ice-cold water through 180 degrees, or up to boiling 
[that is, 900 Btu were evolved]. In experiment No. 3, the heat generated 
in half an hour would have brought 5.31 Ib of ice-cold water to the 
boiling temperature [that is, about 960 Btu were evolved]. But, in this 
last-mentioned experiment, the heat generated was more effectually 
confined, and so less of it was lost; this accounts for the difference in the 
results of the two experiments. 

It remains for me to give an account of one more experiment that was 
made with this apparatus. I found, by experiment No. i, how much 
heat was generated when the air had free access to the metallic surfaces 
which were rubbed together. By experiment No. 2, I found that the 
quantity of heat generated was not sensibly diminished when the air did 
not have free access. Experiment No. 3 indicated that the generation of 
the heat was not prevented or retarded by keeping the apparatus im- 
mersed in water. But, in this last-mentioned experiment, the water, 
though it surrounded the hollow metallic cylinder on every side, ex- 
ternally, was not suffered to enter the cavity of its bore (being prevented 
by the piston) and consequently did not come into contact with the 
metallic surfaces where the heat was generated. To see what effects 
would be produced by giving the water free access to these surfaces, I 
now made the next experiment. 

Experiment No. 4 

The piston which closed the end of the bore of the cylinder being 
removed, the blunt borer and the cylinder were once more put together; 
and the box being fixed in its place and filled with water, the machinery 
was again put in motion. 

There was nothing in the result of this experiment that renders it 
necessary for me to be very particular in my account of it. Heat was 
generated as in the former experiments, and, to all appearance, quite as 
rapidly; and I have no doubt but the water in the box would have been 
brought to boil had the experiment been continued as long as the last. 
The only circumstances that surprised me was to find how little differ- 
ence was occasioned in the noise made by the borer in rubbing against 
the bottom of the bore of the cylinder, by filling the bore with water. 


This noise, which was very grating to the ear, and sometimes almost in- 
supportable, was, as nearly as I could judge of it, quite as loud and as 
disagreeable when the surfaces rubbed together were wet with water as 
when they were in contact with air. 

By meditating on the results of all these experiments, we are naturally 
brought to that great question which has so often been the subject of 
speculation among philosophers, namely, what is heat? Is there any 
such thing as an igneous fluid? Is there anything that can with propriety 
be called caloric^ 

We have seen that a very considerable quantity of heat may be excited 
in the friction of two metallic surfaces, and given off in a constant 
stream or flux in all directions without interruption or intermission, and 
without any signs of diminution or exhaustion. From whence came this 

Was it furnished by the small particles of metal, detached from the 
larger solid masses, on their being rubbed together? This, as we have 
already seen, could not possibly have been the case. 

Was it furnished by the air? This could not have been the case; for, 
in three of the experiments, the machinery was kept immersed in 
water and access to the air of the atmosphere was completely prevented. 

Was it furnished by the water that surrounded the machinery? That 
this could not have been the case is evident: first, because this water was 
continually receiving heat from the machinery, and could not at the 
same time be giving heat to it; and, second, because there was no chem- 
ical decomposition of any part of this water. Had any such decomposi- 
tion taken place (which, indeed, could not reasonably have been ex- 
pected), one of its component elastic fluids most probably inflammable 
air [hydrogen] must at the same time have been set at liberty, and, 
in making its escape into the atmosphere, would have been detected. 
But though I frequently examined the water to see If any air bubbles 
rose up through it, and had even made preparations for catching them, 
in order to examine them, if any should appear, I could perceive none; 
nor was there any sign of decomposition of any kind whatever, or other 
chemical process, going on in the water. 

Is it possible that the heat could have been supplied by means of the 
iron bar m to the end of which the blunt steel borer was fixed ? Or by the 
small neck of gun metal by which the hollow cylinder was united to the 
cannon? These suppositions appear more improbable even than either of 
those before mentioned; for heat was continually going off, or out of the 
machinery, by both these passages, during the whole time the experiment 

And, in reasoning on this subject, we must not forget to consider that 
most remarkable circumstance, that the source of the heat generated by 
friction in these experiments appeared to be inexhaustible. 

It is hardly necessary to add that anything which any insulated body, 

188 CASE 3 

or system of bodies, can continue to furnish without limitation, cannot 
possibly be a material substance ; and it appears to me to be extremely 
difficult, if not quite impossible, to form any distinct idea of anything 
capable of being excited and communicated in the manner in which 
heat was excited and communicated in these experiments, except it be 


Here Rumford emphasizes what he considers to be the chief result 
of these experiments, namely, that the source of the heat generated in 
friction experiments is inexhaustible. If heat were rubbed out of an 
object by friction, as the calorists claimed, a stage should eventually be 
reached in which all the heat in the object would be exhausted. But no 
such stage was ever observed. It was possibly because of the convincing 
character of this chief result that Rumford did not trouble to carry out 
the additional experiments on the heat of fusion of the chips and bulk 
metal mentioned in our note on page 175. 

Rumford points out that, if an insulated object can continue to furnish 
heat without limitation, then heat cannot possibly be a material sub- 
stance. His argument here could have been set forth as follows: if heat 
is a material substance, then it must be indestructible and uncreatable 
(this is the so-called "principle of conservation of caloric," the most basic 
principle of the caloric theory) ; but the present experiments show that 
heat can be created (generated) by friction; therefore, heat is not a 
material substance. Instead, he says, it must be motion which, in the 
present experiments, was communicated to the particles of metal by 
the moving cannon in contact with the fixed borer. 

One supporter of the caloric theory }. B. Emmett (1820) chal- 
lenged the idea that the source of heat in these friction experiments 
was inexhaustible in the sense implied by Rumford. Granting that 
considerable heat is evolved when a metal is rubbed or hammered, 
Emmett contended that this quantity most probably was a small frac- 
tion of the total quantity of heat in the metal. Moreover, the gun metal 
was subject to a large force during the boring and, as the metal wore 
off, a fresh surface was continually being exposed to it. Thus, said 
Emmett, with heat being squeezed out of each fresh layer in succession, 
one should not expect the evolution of heat to cease until all the metal 
was worn away. Rumford continues: 

I am very far from pretending to know how, or by what means or 
mechanical contrivance, that particular kind of motion in bodies which 
has been supposed to constitute heat is excited, continued, and propa- 
gated; and I shall not presume to trouble the Society with mere con- 
jectures, particularly on a subject which, during so many thousand 


years, the most enlightened philosophers have endeavored, but in vain, 
to comprehend. 

But, even though the mechanism of heat should, in fact, turn out to 
be one of those mysteries of nature that are beyond the reach of human 
intelligence, this ought by no means to discourage us, or even lessen 
our ardor, in our attempts to investigate the laws of its operations. How 
far can we advance in any of the paths that science has opened to us 
before we find ourselves enveloped in those thick mists which on every 
side bound the horizon of the human intellect? But how ample and 
how interesting is the field that is given us to explore! 

Nobody, surely, in his sober senses, has ever pretended to understand 
the mechanism of gravitation; and yet what sublime discoveries was our 
immortal Newton enabled to make, merely by the investigation of the 
laws of its action! The effects produced in the world by the agency of 
heat are probably just as extensive, and quite as important, as those 
which are due to the tendency of the particles of matter toward one 
another; and there is no doubt but that its operations are, in all cases, 
determined by laws equally immutable. 

Before I finish this essay, I would beg leave to observe that, although, 
in treating the subject I have endeavored to investigate, I have made no 
mention of the names of those who have gone over the same ground 
before me, nor of the success of their labors, this omission has not been 
due to any want of respect for my predecessors, but was merely to avoid 
prolixity, and to be more at liberty to pursue, without interruption, the 
natural train of my own ideas. 


In the year following the appearance of Rumford's paper on 
heat produced by friction, Humphry Davy (1778-1829) published "An 
Essay on Heat, Light, and the Combinations of Light.'* It first ap- 
peared in a book entitled Contributions to Physical and Medical 
Knowledge, Principally from the West of England, Collected by 
Thomas Beddoes, M.D. (1799). Beddoes was a physician and had been 
professor of chemistry in Oxford University. 

This essay was concerned in part with the question of heat produced 
by friction and was directed against the caloric theory. Davy appears 
to have become interested in this question several years before he began 
to study physical science systematically, for it is related that in his 
seventeenth year he went with a friend to the river, to show him that 
two pieces of ice could be melted by rubbing them together, the melt- 
ing apparently being due to the heat produced by friction. In this same 
year 1795 Davy was apprenticed to a surgeon-apothecary, and it 
was during this apprenticeship that he began the study of physical 

190 CASE 3 

science. Learning of the experiments of Black and Crawford, he soon 
began to form original views about heat and, four months after be- 
ginning his studies, started the research upon which the present essay 
was based. 

Soon after the essay was published, Davy began to see that it con- 
tained fallacies, and he came to refer to it as his "infant chemical 
speculations." Nevertheless, his arguments about heat produced by 
friction, and the type of experiments that he employed, are in some 
respects more cogent than those of Rumford's. Consequently, in later 
years, when the energy theory of heat was becoming established, vari- 
ous writers began to cite Davy's work as a good example of a con- 
vincing attack on the caloric theory. For instance, J. P. Joule, in his 
famous memoir on the mechanical equivalent of heat [Philosophical 
Transactions, vol. 140 (1850), p. 61], said: 

By rubbing two pieces of ice against one another in the vacuum of an 
air pump, part of them was melted, although the temperature of the 
receiver was kept below the freezing point. This experiment was the 
more decisively in favor of the doctrine of the immateriality of heat, in- 
asmuch as the capacity of ice for heat is much less than that of water. 
It was therefore with good reason that Davy drew the inference that 
"the immediate cause of the phenomena of heat is motion, and the laws 
of its communication are precisely the same as the laws of communica- 
tion of motion." 

It should be pointed out that these comments of Joule's, excepting the 
last sentence, refer to the experiments described in Davy's essay of 
1799, here presented. The quotation in the final sentence is taken from 
a later book of Davy's, his Elements of Chemical Philosophy (1812), 
p. 94. We shall see that Joule's description of Davy's experiment with 
Ice is not accurate; moreover, that similar mistakes occur even in some 
present-day accounts of his work. Apparently they have been copied 
from one book to another over a period of more than a century. 

The portion of Davy's essay presented here represents less than one- 
tenth of the entire work, but is the part that deals with heat produced 
by friction. It is a modified and annotated version, based on the essay 
as it is reprinted in The Collected Wor\s of Sir Humphry Davy, Bart., 
LL.D., F.R.S., edited by his brother, John Davy, M.D., F.R.S. (London, 
1839), vol. II, pp. 9-86. 


Humphry Davy 

Matter is possessed of the power of attraction. Owing to this attraction 
the particles of bodies tend to approach one another and to exist in a 


state of contiguity. The particles of all bodies with which we are ac- 
quainted can be made to approach nearer to one another by peculiar 
means; that is, the specific gravity of any body can be increased by dimin- 
ishing its temperature. Consequently (on the supposition of the impene- 
trability of matter), the particles of bodies are not in actual contact. There 
must therefore act on these particles some other power that prevents 
their actual contact; this may be called repulsion. 

The phenomena of repulsion have been supposed, by most chemical 
philosophers, to depend on a peculiar elastic fluid to which the names 
"latent heat" and "caloric" have been given. The peculiar modes of ex- 
istence of bodies solidity, liquidity, and gaseousness depend (ac- 
cording to the calorists) on the quantity of caloric entering into their 
composition; this substance, insinuating itself between their particles, 
and thus separating the particles from one another and preventing their 
actual contact, is, by the calorists, supposed to be the cause of repulsion. 

Other philosophers, dissatisfied with the evidences produced in favor 
of the existence of this elastic fluid, and perceiving the generation of heat 
by friction and percussion, have supposed heat to be a motion. . . . 

Davy probably was familiar with Newton's great generalization, 
arrived at more than a century earlier, that there exist gravitational 
forces of attraction between all particles of matter. In 18065 Davy made 
the important but then novel suggestion, which was later confirmed, 
that there are also electrical forces between atoms, these being much 
stronger than the gravitational forces. 

Davy's statement that the specific gravity of a body can be increased 
by diminishing its temperature is another way o saying that the body 
shrinks in volume when cooled; the specific gravity of a substance 
may be defined, accurately enough for present purposes, as the ratio of 
the weight of any volume of the substance to the weight of a like 
volume of water. 

Incidentally, there are several substances that expand when cooled 
within certain temperature ranges. For instance, water continuously 
expands while being cooled from 39 down to 32R This so-called 
anomalous expansion of water attracted the attention of Count Rum- 
ford, who investigated it experimentally and described the results in a 
paper entitled "Account of Some New Experiments on the Tempera- 
ture of Water at its Maximum Density" (1805). Here again Rumford's 
primary object seemingly was to obtain additional evidence for his 
attack on the caloric theory, for he concluded: "These experiments 
ought not to be regarded as suitable for determining with great exact- 
ness the temperature at which the density of water is at a maximum, 
but rather as proving that this temperature is really several degrees o 
the thermometric scale above that of melting Ice. n Rumford knew that 

192 CASE 3 

the calorists could satisfactorily explain the contraction of an object 
upon cooling as due to the removal of the caloric from it. But how 
could they explain the fact that, below a certain temperature, water 
expands when caloric is removed from it? Rumford apparently felt 
that this phenomenon of anomalous expansion provided strong evi- 
dence against the caloric theory. However, it should be noted that the 
rival view, that "heat is motion" (in the state of its development in 
Rumford's day) also failed to provide a satisfactory explanation of 
anomalous expansion. 

Davy's phrase, "the impenetrability of matter," evidently refers to 
the impenetrability of the particles themselves. In his day these particles 
(atoms or molecules) were thought to be hard impenetrable 
pellets. So the fact that a body can be reduced in volume by cooling or 
by compressing it indicated that the particles are not in actual contact 
but have space between them. But how can there be space between the 
particles if there is an attractive force that tends to pull them together? 
Apparently, as Davy indicates, there must be some other force acting 
on the particles that tends to push them apart, thus balancing the effect 
of the attractive force. 

Considering the discovery of the true cause of the repulsive power as 
highly important to philosophy, I have endeavored to investigate this 
part of chemical science by experiments: from these experiments (which 
I am now about to describe), I conclude that heat, or the power of re- 
pulsion, is not matter. 

Without considering the effects of the repulsive power on bodies, or 
endeavoring to prove from these effects that it is motion, I shall attempt 
to demonstrate by experiments that it is not matter; and in doing this, I 
shall use the method called by mathematicians, reductio ad absurdum. 

Let heat be considered [for the sake of argument] to be matter, and 
let it be granted that the temperature of a body cannot be increased unless 
its specific heat is diminished from some cause or unless heat is added 
to it from some bodies in contact. 

Now the temperatures of all bodies are raised by friction [by rubbing 
the surface of one body against that of another]. Consequently, this 
increase of temperature must be produced in one of three ways: first, 
either by a diminution of the specific heats of the rubbing bodies owing 
to some change induced in them by friction, a change producing in them 
an increase of temperature; or, second, by heat communicated, as a result 
of a decomposition of the oxygen gas in contact with one or both of the 
rubbing bodies; that is, friction must effect some change in these bodies 
similar to an increase of temperature that enables them to decompose 
oxygen gas, in which case they will afterwards be found to be partially 
or wholly oxidized; or, third, by caloric communicated to the rubbing 


bodies by the other bodies in contact with them; that is, friction induces 
a change in the bodies which enables them to attract caloric from the 
surrounding bodies. 

Now first let us suppose that the increase of temperature produced by 
friction arises from a diminution of the specific heats of the rubbing 
bodies. In this case it is evident that some change must be induced in the 
bodies by the rubbing action, which lessens their specific heats and thus 
increases their temperatures. 

Davy's comments about oxygen, in connection with the second of his 
three working hypotheses, indicate that he was familiar with the work 
of Priestley and Lavoisier; but his reference to "the decomposition of 
oxygen gas" suggests that he regarded oxygen as a compound, not an 
element. This makes his ideas here seem muddled, especially in view 
of his subsequent reference to the oxidation of bodies. Probably he 
means that friction conceivably could produce some change in a body 
enabling it to combine readily with oxygen from the air, in which case 
the heat evolved during this oxidation process might account for the 
observed rise in temperature of the rubbed body. 

Experiment II, which follows, is Davy's first experiment on heat 
produced by friction. Experiment 1^ which appears in an earlier section 
not reproduced here, was an attempt "to demonstrate directly that 
light is not a modification or an effect of heat." 

Experiment 11 

I procured two parallelepipeds of ice (the result of the experiment is 
the same if wax, tallow, resin, or any substance fusible at a low tempera- 
ture be used . . .) of temperature 29 F, and 6 inches long, 2 inches 
wide, and % inch thick: they were fastened by wires to two bars of iron. 
By a special mechanism, their surfaces were placed in contact and were 
kept in continuous and violent friction for some minutes. They were 
almost entirely converted into water, which water was collected and its 
temperature ascertained to be 35 F, after remaining in an atmosphere of 
a lower temperature for some minutes. The fusion took place only at the 
plane of contact of the two pieces of ice, and no bodies were in friction 
but ice. 

From this experiment it is evident that ice by friction is converted 
into water, and according to the supposition of the calorists, its specific 
heat is diminished. But it is a well-known fact that the specific heat of 
ice [which is 0.5 Btu/lb F] is much smaller than that 'of water; more- 
over, that a definite quantity of heat [namely, 144 Btu/lb] must be 
added to ice to convert it into water. Friction consequently does not 
diminish the specific heats of bodies. 

From this experiment it is likewise evident that the increase of temper- 
ature consequent on friction cannot be due to the decomposition of the 

194 CASE 3 

oxygen gas In contact, for ice has no [chemical] attraction for oxygen. 
Since the increase of temperature consequent on friction cannot be due 
to the diminution of specific heat, or to oxidation of the rubbing bodies, 
the only remaining supposition is that it arises from a quantity of heat 
added to them, which heat must be attracted from the bodies in contact. 
On this supposition friction must induce some change in bodies that 
enables them to attract heat from the bodies in contact. 

In other words, Davy chose for this experiment a material ice 
that he knew would not oxidize, thus automatically disposing of the 
possibility that the heat produced by rubbing pieces of ice together was 
due to oxidation. 

Davy's argument about melting ice by friction is perhaps even more 
convincing than was one of Rumford's in the cannon-boring experi- 
ment (Sec. 4). Rumford, it will be recalled, showed experimentally 
that the specific heat of the metallic chips abraded during the boring 
of the cannon was not sensibly different from that of the solid metal; 
thus he refuted one of the claims of the calorists, namely, that the 
heat evolved is the result of a diminution in the specific heat of the 
abraded material. In Davy's experiment we can think of the melted 
ice (water) as playing a role similar to that of Rumford's chips; and 
not only is heat absorbed, rather than released, during the melting, but 
the specific heat of this melted ice, instead of being less than that of ice, 
or even equal to it, is twice as large. So Davy was right in thinking it 
important to determine whether heat is evolved when ice is subjected 
to friction. The calorists would have found it hard to explain how an 
increased specific heat could result in the evolution of heat. 

Although we know today that heat is produced, with consequent 
melting, when two pieces of ice are rubbed together, Davy's experiment 
II actually was incapable of yielding convincing evidence on this 
question. As the British physicist E. N. da C. Andrade has pointed out, 
in the periodical Nature, vol. 135 (1935)? p. 359? if the rubbing surfaces 
of the ice contain a film of water, the frictional force is small and little 
heat is produced; therefore, since the heat of fusion of ice is large 
(144 Btu/lb), hardly any ice would melt as a result of the rubbing. 
On the other hand, if the ice is dry, it tends to stick together, thus 
slowing down or even stopping the rubbing process. Another compli- 
cation is that force necessarily must be employed to hold the two 
blocks of ice together, and this lowers slightly the melting temperature 
of the ice, causing it to melt at the surfaces of contact even when these 
surfaces are not being rubbed together. Moreover, some of the resulting 
water flows to the edges, where the pressure is lower, and there it 
freezes again, thus causing the two blocks to cohere; this phenomenon, 


which is called re gelation, may have been unknown or, at least, not 
well understood in Davy's day. 

Davy says that the two blocks of ice were "after some minutes . . . 
almost entirely converted into water, . . . and its temperature [was] 
ascertained to be 35 F." To melt this much ice and raise the tempera- 
ture of the resulting water several degrees requires a much larger 
quantity of heat than was likely to have been produced by the friction. 
Therefore, as Andrade says, the effect observed by Davy was doubtless 
due almost entirely to conduction of heat from the surroundings. 
Andrade adds: "It does not detract from the greatness of Davy to point 
out that his first experiments, carried out in 1799 while he was still a 
country lad, were uncritical and lacked all quantitative basis." 

In experiment III, which follows, Davy tries to determine whether 
the heat "collected by friction" is coming from other objects in contact 
with the rubbing bodies. 

Experiment III 

I procured a piece of clockwork so constructed as to be set to work in 
an evacuated vessel; one of the external wheels of this machinery came in 
contact with a thin metallic plate. A considerable degree of sensible heat 
[as indicated by a rise in temperature] was produced by friction between 
the wheel and plate when the machine worked uninsulated from bodies 
capable of communicating heat. 

I next procured a small piece of ice and round its upper edges made 
a small canal which I filled with water. The machinery was placed on 
the ice, but not in contact with the water. Thus disposed, the whole was 
placed in the vessel attached to the vacuum pump. This vessel had been 
previously filled with carbonic acid gas [carbon dioxide], a quantity of 
potash (that is, caustic vegetable alkali) [potassium hydroxide] being 
at the same time introduced. 

The vessel was now evacuated. This evacuation, together with the 
attraction of the carbonic acid gas by the potash, produced a nearly 
perfect vacuum, I believe. 

Carbon dioxide gas (CO 2 ) was put in the vessel so as to expel the 
air. Then potassium hydroxide (KOH) was introduced; it combined 
chemically with the carbon dioxide to produce potassium acid carbon- 
ate (KHCO 3 ), which is a nonvolatile solid substance and thus helped 
to evacuate the vessel. Even with modern high-vacuum pumps, which 
are immensely superior to the pumps available to Davy, refrigerants 
and materials called "getters'* are often used to remove water vapor 
and other gases that cannot easily be removed by a pump. 

As the next two paragraphs indicate, Davy used wax, not ice, as the 
substance to be melted in this experiment, a fact that he has not previ- 

196 CASE 3 

ously mentioned. Apparently the wax was attached to the "thin metallic 
plate" (it may have been a metallic dish or tray) against which one of 
the clockwork-driven wheels rubbed. The purpose of the block of ice 
was to insulate the machinery from surrounding objects. 

The machinery was now set to work. The wax rapidly melted, show- 
ing that there was an increase of temperature. 

Note. The temperature of the ice, machinery and surrounding atmos- 
phere at the commencement of the experiment was 32?. At the end of 
the experiment the temperature of the coldest part of the machinery was 
nearly 33 F, and that of the ice and surrounding atmosphere was the 
same as at the commencement of the experiment; so the heat produced 
by the friction of the different parts of the machinery was sufficient to 
raise the temperature of almost half a pound of metal at least iF and 
to melt 18 grains of wax (the quantity employed). 

Caloric therefore was collected by friction; and this caloric, on the 
afore-mentioned supposition, was communicated to the machinery by 
the bodies in contact with it. But in this experiment, ice was the only 
body in contact with the machinery. Had this ice given out caloric, the 
water in the canal on the top of it would have frozen. But this water was 
not frozen; consequently, the ice did not give out caloric. Nor could the 
caloric have come from the other bodies in contact with the ice; for it 
would have had to pass through the ice to reach the machinery, and an 
addition of caloric to the ice would have converted it into water. 

Davy says that enough heat was furnished in experiment III to in- 
crease the temperature of half a pound of metal at least iF and to 
melt 1 8 grains of wax. Assuming that the "metal" was iron and that 
the "wax" was beeswax, one can easily show that the quantity of heat 
evolved was only about 0.06 Btu. If it were the water in the channel 
that had furnished this heat, (0.06/144) Ib of it would have frozen 
about 3 grainsl As Andrade says (loc. at.), the production of so small a 
weight of ice "actually could not have been observed by the eye in this 
experiment. The experiment proves nothing at all." In fact, so far as 
this particular experiment is concerned, one could just as easily arrive 
at the contrary conclusion, namely, that the heat "collected by friction" 
did come from the ice. To do this, one need only assume that 3 
grains of water did freeze, but could not be seen with the eye. It seems 
evident that Davy did not carry out the foregoing computation, or he 
would have seen for himself that the experiment lacked quantitative 

Thus heat, when produced by friction, cannot be collected from the 
bodies in contact. Moreover, it was proved by experiment II that the 
increase of temperature consequent on friction cannot arise from a 


diminution of specific heat or from oxidation. But if heat be considered 
as matter, it must be produced in one of these three ways. Since (as is 
demonstrated by these experiments) it is produced in none of these ways, 
it cannot be considered as matter. It has thus been experimentally demon- 
strated that caloric, or the matter of heat, does not exist. 

Solids expand when subjected to prolonged and violent friction (ex- 
pansion by friction is common to almost all bodies; and as the exceptions 
are very few, it may be admitted as a principle . . .) and, if they are of 
a higher temperature than the human body, affect the sense organs with 
the peculiar sensation known by the common name of heat [warmth, 
or hotness]. Since bodies become expanded by friction, it is evident that 
their particles must move away, or separate, from one another. Now, a 
motion or vibration of the particles of bodies must be necessarily gen- 
erated by friction and percussion. Therefore we may reasonably conclude 
that this motion or vibration is heat, or the repulsive agent. 

Heat, then, or that power which prevents the actual contact of the 
particles of bodies, and which is the cause of our peculiar sensations of 
heat and cold, is to be regarded as a peculiar motion, probably a vibra- 
tion, of the particles of bodies, tending to separate them. It may with 
propriety be called the repulsive motion. 

Despite the fact that experiments I and II lack quantitative signifi- 
cance, Davy's main conclusion is now known to be correct: heat is due 
to "a peculiar motion ... of the particles of bodies." Possibly he felt so 
sure of the correctness of this view that he was careless or even preju- 
diced in his observations, and hasty in his generalizations. In his youth- 
ful enthusiasm he had tried to perform experiments that would tax the 
ingenuity of a trained experimental physicist using much more modern 

Davy later realized that he had shown poor judgment in rushing into 
print at a time when he lacked experience and critical judgment in ex- 
perimentation. Yet there is another side to this question, which is well 
illustrated by something said by Benjamin Franklin in a letter to Peter 
Collinson, reproduced in I. B. Cohen's Benjamin Franklin's Experi- 
ments (Harvard University Press, 1941), p. 279: 

These thoughts, my dear friend, are many of them crude and hasty; 
and if I were merely ambitious of acquiring some reputation in philos- 
ophy, I ought to keep them by me till corrected and improved by time, 
and farther experience. But since even short hints and imperfect experi- 
ments in any new branch of science, being communicated, have often- 
times a good effect, in exciting the attention of the ingenious to the 
subject, and so become the occasion of more exact disquisition, and more 
compleat discoveries, you are at liberty to communicate this paper to 
whom you please; it being of more importance that knowledge should 
increase, than that your friend should be thought an accurate philosopher. 

198 CASE 3 

It was not until some 40 years after the experiments o Rumford and 
Davy that the subject o heat produced by friction was reinvestigated in 
a new and quantitative way by J. R. Mayer, in Germany, J. P. Joule, in 
England, and others; and by 1850 these investigators had established 
beyond much doubt that heat is not a separate substance, or fluid, but 
is kinetic energy associated with the motions of the small particles of 
ordinary matter. However, many scientists continued to favor the caloric 
theory and, as late as 1856, it received preference over the energy theory 
in the article "Heat" in the Encyclopedia Britannica (ed. 8). 

Even today we sometimes find it useful and convenient to think of 
heat as a fluid, as when we speak of heat "flowing" from one object to 
another, or of an object "soaking up" heat. Many modern calorimetric 
determinations, for example, can be carried out just as well by thinking 
of heat as an indestructible fluid as by thinking of it as energy. An anal- 
ysis of such experiments will show that the procedures employed in 
them do not depend on any assumption concerning the ultimate nature 
of heat except that heat is conserved. Such procedures are possible when 
there is no appreciable transformation of heat from, or into, any other 
form of energy. 

Rumford's conclusion, stated in his paper of 1798, that heat is motion 
acquired additional significance a half-century later, when it became 
clear that heat is a form of energy the kinetic energy associated with 
the random motions of the atoms and molecules comprising all matter. 
Some such notion of the nature of heat must have occurred to the earlier 
advocates of the mode-of-motion theory, especially those who were 
familiar with seventeenth- and eighteenth-century developments in 
mechanics. As early as 1695, G. W. Leibniz, the German mathematician 
and philosopher, had suggested that the diminution of vis viva (essen- 
tially what we now call kinetic energy) observed when two inelastic 
bodies collide "happens only in appearance." It is "not destroyed, but 
dissipated among the parts. That is not to lose it, but to do like those 
who change large money into small" Certainly by 1780 this notion 
had been rendered explicit, for Lavoisier and Laplace, in their Memoir e 
sur la Chaleur (1780), called attention to the opinion that "heat is the 
vis viva resulting from the insensible movements of the particles of a 
body. It is the sum of the products of the mass of each particle by the 
square of its velocity." 

But these early speculations were not based on quantitative experi- 
mentation. Thermal science and mechanics still were almost completely 
separate disciplines, and seemingly it had not occurred to anyone to try 
to correlate them by seeking quantitative relations between thermal and 
mechanical quantities, such as quantity of heat (expressed in British 
thermal units) and mechanical energy (expressed in foot pounds). In- 


deed, it was experiments like those of Rumford's that were needed to 
establish this relation, although their significance in this respect ap- 
parently escaped his notice. 

Rumford says (p. 185) that his machinery "could be driven by the 
force of one horse." Whether he had in mind here the mechanical work 
done by the horse is not clear; for in his day the word "force" had a 
troublesome double meaning, sometimes being used to denote force in 
the present-day sense of the term, but more frequently, to denote the 
concept that we now call mechanical wor\. He does point out that heat 
was evolved as long as the horse continued to act, and he obtained data 
(p. 1 83) which show roughly that the quantity of heat evolved was di- 
rectly proportional to the time during which the horse acted. But he 
does not state or discuss this relation in his conclusions, or say anything 
to indicate that he realized its significance. 

Some physiologists and medical men of the period saw significance 
in Rumford's results in connection with their studies of the sources of 
animal heat. The physical scientists, on the other hand, were under- 
going a reaction to a highly speculative philosophy of nature which had 
strongly influenced them for the past several decades; so they were 
currently more interested in conscientious factual research than in what 
appeared to them to be mere speculation about the ultimate nature of 
heat. Recognition of the importance of the latter problem therefore 
came only in a later stage of the industrial revolution, when steam 
engines of improved efficiency were coming into wide use for driv- 
ing machines. Then the need for correlating the heat and the me- 
chanical work involved in such devices became more obvious and 

The cannon-boring apparatus clearly was not designed for the pur- 
pose of establishing a precise quantitative relation between heat and 
work. Certainly Rumford was aware that the apparatus had shortcom- 
ings, but he evidently felt that it served his main purpose, which was 
both here and in many other of his experiments performed during a 
30-year period to attack the currently accepted caloric theory from 
as many different points of view as seemed possible. A few years later 
he designed a simpler and more compact device for showing the pro- 
duction of heat by friction, which he described in his Mcmoire sur la 
Chaleur (Paris, 1804). He felt that the large-scale experiments made in 
the arsenal might not be convincing unless they could be repeated by 
other investigators. This new apparatus, which was cleverly designed 
and easily could have been adapted to quantitative measurements, was 
very similar to one of a number of devices developed more than half 
a century later for the express purpose of checking and rechecking the 
relation between the British thermal unit and the mechanical unit of 

200 CASE 3 

energy called the foot pound. This relation, which must be determined 
experimentally, came to be called the mechanical equivalent of heat. 

To illustrate how Rumford's cannon-boring data could have been 
used to make a rough but explicit determination of the mechanical 
equivalent of heat, consider experiment No. 3. There the quantity of 
heat produced by friction in 2.5 hr, or 9000 sec, was 4900 Btu. Thus the 
average quantity of heat produced during each second of operation was 
4900 Btu/9ooo sec, or 0.540 Btu/sec. Now earlier than the time of the 
present experiments, in about 1783, James Watt had made some esti- 
mates which indicated that a "mill horse" could exert a steady pull of 
150 Ib in the direction in which it was moving while walking with a 
velocity of 2.5 mi/hr; in other words, it could do mechanical work at 
the rate of 550 foot pounds per second. Assuming that Rumford used 
a "mill horse," we can equate the rate of evolution of heat to the rate 
at which the horse worked. Thus, 0.540 Btu/sec = 550 ft Ib/sec, or 
i Btu = (550/0.540) ft Ib = 1000 ft Ib. In Rumford's day this result 
probably would have been expressed in words similar to the following: 
the quantity of heat capable of increasing the temperature of a pound 
of water by one degree of Fahrenheit's scale is equivalent to the work 
done in raising a looo-lb object through a vertical distance of one foot. 

Rumford did not make the foregoing calculation, or even suggest the 
possibility of making it. Very likely he was not aware of Watt's esti- 
mate of 550 ft Ib/sec for the power of a horse, for the latter had recorded 
it in longhand in one of a series of notebooks in which he was in the 
habit of making notes and calculations from time to time. A printed 
reference to Watt's estimate appeared in a book review in the Edinburgh 
Review in 1809, more than a decade after Rumford wrote the present 
paper; but Watt's own account of his estimate was not published until 
1818, several years after Rumford's death. 

The first determinations of the mechanical equivalent of heat of 
which there are published records were made by J. R. Mayer (1842) 
and J. P. Joule (1843). The presently accepted value is 777.9 ft Ib/Btu. 
Once an exact and unvarying relation between mechanical work and 
the quantity of heat into which it may be converted was established, 
the further step of introducing the hypothesis that heat itself is a form 
of energy was not difficult. 


i. Evolution of the thermometer 

1. Prepare a chronologic epitome of thermometry, with the entries ar- 
ranged and worded somewhat as follows: ca. 1595. Air-expansion barother- 
moscope invented by Galileo. 

2. Fahrenheit devised a fever thermometer that was known as a "pyran- 
thropometer." Is this name suggestive of the purpose for which the instru- 
ment was intended? 

3. Why was Fahrenheit's substitution of a cylindrical for a spherical bulb 
an improvement? 

4. Cite evidence from the foregoing brief history of the thermometer or 
from your other readings that appears either to substantiate or to refute each 
of the following statements taken from recent books or periodical articles: 
(i) "Boyle devised a thermometer utilizing aniseed oil as the theraiometric 
substance"; (ii) "Boyle's experience in other parts of physical science were 
of such nature as to make him well qualified for thermometric studies"; 
(iii) "Two fixed points are an absolute necessity if the degrees of tempera- 
ture are to be definitely defined"; (iv) "It may well be that, from Galileo's 
air-expansion instrument, one could trace two historical threads of develop- 
ment, one leading to thermometers, the other to barometers"; (v) "In study- 
ing the origin of certain discoveries, one is often perplexed by encountering 
several claimants for priority. This may be because two or more persons 
independently reach the same result at about the same time; or because of 
the effort of each nation to secure credit and renown for its own people; or 
because of the failure of the discoverer to claim priority owing to the fact 
that he himself failed to appreciate its importance and utility"; (vi) "A cen- 
tesimal thermometric system was first suggested by Anders Celsius, in 1642, 
but it differed from the modern centigrade system in that the values o and 
100 were assigned to the steam and ice points, respectively, instead of the 
other way around"; (vii) "For weather reports and many everyday pur- 
poses, the Fahrenheit system has the advantages over other systems that the 
observer seldom has to record negative readings and also can make closer 
readings without having to estimate fractions of a degree." 

5. (a) Show that F = C + 32, where F is any temperature expressed 

in the Fahrenheit system and C is the same temperature expressed in the 
centigrade system. (b) Use the foregoing equation to find the values of F 
equivalent to the following values of C: -40C, oC, 50C, 100 C. (r) On 
a sheet of graph paper plot these four values of F as ordinates, and the cor- 
responding values of C as abscissas; for both the horizontal and vertical 
scales of the graph, let i mm, say, represent i deg of temperature, (d) Use 
your graph to find the temperature in degrees Fahrenheit that corresponds 

202 CASE 3 

6. In the thermometric system devised in 1731 by R. A. F. Reaumur, and 
still used to some extent in Germany, the ice point and steam point have the 
values oR and 8oR, respectively, (a) Show that 68F is equivalent to 

i6R. (#) Derive the conversion formula C = R, where the symbols C 


and R represent the same temperature expressed in the centigrade and 
Reaumur systems, respectively. 

7 A. J. N. Delisle, a French astronomer, employed a thermometric system 
in about 1735 in which the ice and steam points were called 150 and o, re- 
spectively, (a) Show that a reading of 140 in this system is equivalent to 

44 F. () Derive the conversion formula D = 150 C, where D and C 

represent the same temperature expressed in the Delisle and centigrade sys- 
tems, respectively. 

8A. In 1731, R. A. F. Reaumur set up a thermometric scale and system by 
using an alcohol-in-glass expansion thermometer having the ice point 
(marked oR) as a single fixed point and having successive degrees, each 
of which represented an expansion of i/iooo the volume of the alcohol at 
the ice point. He found that the alcohol expanded from 1000 to 1080 vol- 
umes between the ice point and the steam point, thus giving 80 R for the 
latter temperature, (a) Would the degree marks on such a thermometer be 
equal distances apart? (#) Devise a method for determining whether the 
bore of a glass tube to be used in making a thermometer is of uniform cross- 
sectional area. 

9A. It is often pointed out that the expansion of mercury with increase in 
temperature is exceedingly regular, (a) Suggest an experiment that would 
serve to test the correctness of this statement. () If, in this experiment, you 
wished to use a mercury-in-glass thermometer to measure the temperature, 
how would you calibrate it? 

2. Joseph Blacks discoveries of specific and latent heat 

10. How does Black's conception of "equilibrium of heat" differ from the 
earlier idea of "equal heat"? 

11. (a) Using Black's correct formula our Eq. (4) show that the 
quantity of heat required to warm 10 Ib of water from 32 to 2i2F is 1800 
Btu. () Why it is better to express this result as 18 X *o 2 Btu? 

12. Which of these two definitions is the more acceptable, and why? (i) 
Given that two objects, A and B> are in contact, and that A is observed to be 
at a higher temperature than #, we define the direction of flow of heat as 
being from A to B. (ii) Given that heat is observed to flow from object A 
to object B y we define A as being at a higher temperature than B. 

13. Is there any way to make a direct experimental test of the principle of 
conservation of heat, or can it be verified only by making deductions from 
it and subjecting the latter to experimental tests? 


14. Referring to Marline's experiment with water and mercury (p. 134), 
state: (a) the hypothesis and deductions that led him to make this experi- 
ment; (b) the factors that he considered relevant in planning it; (c) other 
factors that he might have considered relevant, and why he may have ig- 
nored them; (d} the factors that he tried to keep constant, and the variables 
that he measured; (e) the main conclusions. 

15. Fahrenheit found that the mixing of equal volumes of mercury ini- 
tially at 150? and of water initially at iooF resulted in a mixture tempera- 
ture of i20F. (a) Use Black's correct formula our Eq. (4) to compute 
the value for the specific heat of mercury given by this experiment, (b) What 
is the percentage difference between this value and the modern one? 

1 6. In an experiment not described in the present excerpts, Black put a 
lump of ice into an equal weight of water of initial temperature I76F and 
found that, after the ice had melted, the mixture "was no hotter than water 
just ready to freeze." (a) Show that the value for the heat of fusion of ice 
yielded by these data is 144 Btu/lb. (b) Would this value be made larger or 
smaller if account could be taken of the heat lost to the mixture by the hot 

17. In the method-of-mixtures experiment on the melting- of ice (p. 144), 
suppose that Black, like his predecessors, had failed to take into account the 
4.8 Btu of heat lost by the hot glass. What value would he then have ob- 
tained for the heat of fusion of ice? 

1 8. Show that, after Black made his several discoveries, it was no longer 
acceptable to define heat qualitatively as that which always increases the 
temperature of a body to which it is added. 

19. (a) Make a list of the main working hypotheses that are mentioned in 
connection with Black's work on specific and latent heats, (b} Which of 
these turned out to be incorrect? (c) Which of them are broad enough to 
be regarded as conceptual schemes? 

20. What evidence 3 if any, can you find in Black's work in support of each 
of the following generalizations: (i) the development of a new instrument 
of measurement may lead to many new discoveries; (ii) the mere amassing 
of observational and experimental data does not constitute advance in a 
science; (iii) a new experimental technique may arise from, or be improved 
on, from a consideration of a practical art; (iv) new concepts may result 
from experiments or observations; (v) it is important to distinguish be- 
tween a new concept and the explanation of this concept; (vi) a working 
hypothesis often is formulated as the result of relatively few observations, 
all of which may be no more than semiquantitative in character. 

21. Although Black clearly understood the distinction between the con- 
cepts of temperature and heat, he often used various exact synonyms for 
temperature, such as "degree of hotness," "strength of heat," "heat of a 
body," and "intensity of heat/' (a) Which of these synonyms probably first 
came into use before his time, when temperature and heat were badly con- 
fused? (b) Do you know of other synonyms for temperature that are still 
in everyday use? (c) Do you know of any nonscientific words in ordinary 

204 CASE 3 

language that are exact synonyms? (d) Why do exact synonyms occur so 
frequently in the sciences, especially the physical sciences? (e) What is your 
opinion of the tendency in modern scientific literature to avoid using syno- 
nyms for scientific concepts for example, always to use the term tempera- 
ture in referring to this concept? (/) Are there any kinds of extrascientific 
literature for which adoption of this practice by authors should be en- 
couraged ? discouraged ? 

22. Some writers have asserted that Black developed the theory and ex- 
perimental procedures of heat measurements in response to a practical de- 
mand for such knowledge in the further development of steam engines. What 
evidence can you find for or against this assertion? 

23. How do you account for the fact that Black was able to make his im- 
portant discoveries of specific and latent heats while favoring a theory of 
heat the material, or caloric, theory that is now known to be incorrect? 

24. Black warned Robison, as a student, "to suspect all theories whatever 
. . . and to reject, even without examination, every hypothetical explanation 
as a mere waste of time and ingenuity." (a) How can this advice of Black's 
be reconciled with the fact that he developed a theory of heat measurements 
involving concepts, working hypotheses and axioms? (b) In what sense 
was he probably using the phrase "hypothetical explanation"? 

25. How much heat is transferred to surrounding, colder objects: (a) 
when 20 Ib of liquid in (p. 146) at 450 F freezes to solid tin of the same 
temperature? (#) when 10 Ib of steam at 2i2F condenses to water of tem- 
perature 60 F? 

26 A. Fahrenheit found that the mixing of 3 volumes of mercury at i50F 
with 2 volumes of water at iooF resulted in a mixture temperature of 
125 F. (a) Compute the specific heat of mercury from these data, (b) What 
is the percentage difference between this value and the modern one? 

27 A. (a) Prove that it follows from the erroneous weight hypothesis 
our Eq. (i) that the quantity of heat required to produce a temperature 
rise A* in any body of weight w is given by the equation H cwkt, 
where c is a proportionality factor supposedly having the same value for all 
substances, (b) Prove that it follows from Boerhaave's erroneous volume 
hypothesis our Eq. (3) that H = /FA/, where c supposedly is the 
same for all substances, (c) Show that if the first of the foregoing equations 
is applied to the mixing of equal volumes of water at iooF and mercury at 
I50F, the predicted mixture temperature will be I40F, instead of the 
I20F actually observed by Fahrenheit. (J) What mixture temperature is 
predicted by the second equation? 

28A. When a certain liquid of specific heat s^ and weight w-i is placed in 
a vessel and exposed to a steady source of heat, the temperature of the liquid 
is observed to rise through 10 Fahrenheit degrees in a time TV When the 
experiment is now repeated with the same vessel, but with another liquid 
of specific heat s% and weight w^ the temperature is observed to rise through 
10 Fahrenheit degrees in a time T 2 , Assuming that heat is supplied at the 
same constant rate in both experiments, show that 


+ S 

where S is the quantity of heat required to raise the temperature of the 
vessel through i Fahrenheit degree, (b) On the supposition that S for each 
of the glass vessels used by Martine (p.i34) was 0.012 Btu/F, compute the 
ratio Ti/Tz for the equal volumes of mercury and water which he warmed 
through the same temperature interval, (c) How does this value compare 
with Martine's and also with the value 2.5 obtained in question 29 A? 

2pA. In an experiment similar to that of Martine's, equal volumes of mer- 
cury and water are exposed to the same steady fire. Given that the specific 
heat of mercury is 0.033 Btu/lb F and that mercury is 13.6 times as dense 
as water, show that: (a) to produce the same temperature rise in both liq- 
uids, only 0.4 as much heat must be added to the mercury as to the water, 
and (b) the mercury warms 2.5 times as fast as the water, (c) Martine, a 
careful experimenter who had good thermometers, observed that the mer- 
cury warmed a little less than twice as fast as the water. Can you account 
for the discrepancy between this observed value and the computed value 
of 2.5? 

3oA. In one experiment on vaporization that is omitted from these ex- 
cerpts, Black found that 0.55 Ib of water warmed from 50 to 2izF in 3.5 
min, and all boiled away in 18 rnin more. Show that: (a) heat entered the 
water from the "red-hot kitchen table" at an average rate of 25.4 Btu/min 
and (b) the value for the heat of fusion of water given by this experiment 
was 830 Btu/lb. 

3 1 A. Which postulate, or postulates, of the caloric theory (p.i55) can be 
used to "explain" each of the following phenomena: (a) a body generally 
expands when warmed; (b} a hot object tends to lose heat to the cooler sur- 
roundings; (c) all bodies conduct heat, but some better than others; (d) 
specific heats differ for different substances and different states of aggrega- 
tion; (e) heats of fusion and vaporization differ for different substances; 
(/) bodies of different initial temperatures tend to acquire a common tem- 
perature when mixed; (g) heat can be produced by friction or percussion; 
(h) water expands when it freezes; (i) some substances contract upon 

32A. Aside from his orally delivered lectures to students and two papers 
read at club meetings in Glasgow, which were not preserved, Black seem- 
ingly never gave any public account of his discoveries in heat. How is his 
failure to publish explained by historians, and what consequences do they at- 
tribute to it? (See, especially, references 23, 28, and 29 in our Bibliography.) 

3. Count Rumford's investigation of the weight ascribed to heat 

33. What does Rumford mean by "philosophical investigation" ( p. 1 60)? 

34. On page 160 Rumford refers to weights that were "exactly equal" and 
to balance arms having lengths "of the most perfect equality." How nearly 

206 CASE 3 

equal do two weights or two lengths have to be in order to be "exactly" or 
"perfectly" equal? 

35. (a) What observations eventually led Rumford to suspect that his 
first experiments with water and alcohol (pp. 159 ff) were not dependable? 
() Does he ever satisfactorily explain why the water appeared to increase 
in weight upon freezing? 

36. How does Rumford's value for the specific heat of mercury (p. 163) 
compare with the modern value of 0.033 Btu/lb F? 

37. In one experiment (p. 162), 0.57 Ib of water and an equal weight of 
mercury were cooled from 61 to 34F. (a) Compute the quantity of heat 
given off by each liquid. () In what ways was this experiment superior to 
those of earlier experimenters in which a single metal was heated? 

38. In view of Rumford's remarks about the accuracy of his balance (p. 
163^ would he have been able to measure a difference in weight if it had 
been as small as 0.0002 percent? If it had been o.oooi percent? 

39. (a} List all the possible sources of error that Rumford took into ac- 
count in his final experiment with water, alcohol and mercury (pp. 164 ft), 
(b) In what respects was this experiment superior to his earlier ones? (c) 
Why did he think it unnecessary to place a thermometer in the bottle con- 
taining the mercury? 

40. What reasons did Rumford have for thinking that changes in atmos- 
pheric pressure and density could not affect the apparent weights in his 

41. For each of Rumford's experiments, state: (a) the hypotheses and 
deductions that led him to make the experiment; (b) the factors that he 
considered relevant in planning it; (c) other factors that he might have 
considered relevant, and why he may have ignored them; (d) the factors 
that he tried to keep constant, and the variables that he measured or ob- 
served; (e) the conclusions. 

42. In Fordyce's experiment and Rumford's first experiment, suppose 
that the increase in weight of the water upon freezing had actually turned 
out to be due to "the weight of heat" instead of to some "accidental cause." 
How might the calorists have explained an increase in the weight of an 
object when heat is removed from it? 

43. What criticisms can be made of Tilloch's argument (p. 167) ? 

44 A. (a) In the first experiment (pp. 159 ft), 0.59 Ib of water and an equal 
weight of alcohol were cooled from. 61 to 29 F. Assuming that the specific 
heat of the alcohol was 0.6 Btu/lb F, compute the quantities of heat lost 
by the water and by the alcohol, (b) If the observed change in weight ac- 
tually had been due to the "weight of heat," what value would the data for 
this experiment have yielded for the weight of i Btu? 

45 A. In testing the balance (pp. 160 ff), if the beam were in equilibrium 
when no weights were attached to its ends, would this have sufficed to show 
that the two arms of the balance were of equal length? 

4&A. On p. 161 Rumford says that he could have determined whether 
or not the arms of his balance were equal in length by "causing the two 


bottles A and B to exchange places upon the arms of the balance.'* This 
way of testing a balance was later used by Karl Friedrich Gauss (1777-1855) 
as the basis for his method of double weighing, which serves to eliminate 
errors caused by inequality in the lengths of the balance arms. Suppose 
that, when an object is put in one pan of a balance, a known weight W 
must be put in the other pan to balance it; but, when the object is transferred 
to this second pan, a different known weight W is needed in the first pan 
to produce balance, (a) Show, vvith the help of Archimedes' principle of 
the lever, that the weight of the object is given by the expression \/WW. 
(b) Show that, if W and W / have nearly the same value, the foregoing ex- 
pression reduces to -J (1^ + W)> which is simpler to use in computations. 

47A. P. W. Bridgman, in his book, The Logic of Modern Physics (Mac- 
millan, 1927), says: "One of the problems of the future is the self-conscious 
development of a more powerful technique for the discovery of new rela- 
tions without the necessity for preconceived opinions on the part of the ob- 
server." (a) Why might such a technique be advantageous? (b) Why might. 
it be impossible? 

48A. Show that the quantities of heat lost by the water, alcohol, and mer- 
cury in the final experiment (pp. 164 ff) were approximately in the ratios 

of 170 tO 20 tO I. 

49A. An open beaker containing hot water is placed on a sensitive balance 
in a room of temperature 25 F. (a) What various factors could conceivably 
affect the apparent weight of the vessel and contents while they gradually 
cooled to 25 F? () Would your answer be different if the water were en- 
closed in a hermetically sealed flask? 

5oA. A piece of metal has an apparent weight of 3.0 Ib when immersed 
in water of weight-density 62.4 lb/ft 3 . A piece of wood has a true weight of 
1.8 Ib and an average weight-density of 31.2 lb/ft 3 . Show that the metal 
and wood, when fastened together and immersed in the water, will have 
an apparent weight of only 1.2 Ib. 

5 1 A. An empty bottle is hermetically sealed and weighed when immersed 
in water. The bottle is then opened and, after a piece of cork has been en- 
closed in it, is resealed and weighed when immersed, (a) How does the 
combined apparent weight of the bottle and cork compare with the appar- 
ent weight of the empty bottle? () Can you apply this example in a critical 
examination of Tilloch's argument? 

4. Count Rumford's experiments on the source of heat that is excited by 

52. What light, if any, does this paper throw on the role of accident in 
discovery and experimentation? 

53. (a) Is there any indication that Rumford carried out these experi- 
ments primarily to solve a technological problem? (&) Has this paper served 
in any way to enlarge your conceptions of how science and technology are 
related, and of the ways in which each may contribute to the progress of 
the other? 

208 CASE 3 

54. (a) What are the meanings and implications of the words "beautiful" 
and "elegant" when used in such expressions as "beautiful experiment" 
(p. 183), "beautiful theory," and "elegant mathematical proof"? (b) Is Rum- 
ford's acknowledgment of "childish pleasure" (p. 183) suggestive of any 
significant characteristic of the man or, for that matter, of many people 
who are highly creative and productive in their work? 

55. (a) Referring to the final paragraph of the paper (p. 189), comment 
on the advantages and disadvantages of including documentary evidence 
and bibliographic references in a paper intended for oral delivery; in one 
intended for publication, (b) Comment on the possible value of Rumford's 
practice (p. 177, and elsewhere) of carefully specifying the dimensions of 
the apparatus. 

56. (a) Using the data on page 182, carry out the computation needed to 
show that the specific heat of the gun metal was o.n Btu/lb F. (b) Was 
Rumford justified in expressing this result to four significant figures? (c) 
Do the data and experimental method employed warrant the retention of 
two significant figures? 

57. In referring to experiment No. i, Rumford says that the quantity of 
heat evolved during the first 30 min was equivalent to that needed to warm 
5 Ib of water from 32 to 2i2F. Show that: (a) the quantity evolved was 
900 Btu; (b) its rate of production was 0.5 Btu/sec. 

58. For one or more of Rumford's four experiments the one on specific 
heats and Nos. i, 2, and 3 state: (a) the hypotheses and deductions that 
led Rumford to make the experiment; (b) the factors that he considered 
relevant in planning it; (c) other factors that he might have considered 
relevant, and why he may have ignored them; (d) the factors that he tried 
to keep constant, and the variables that he measured or obseived; (c) the 

59. What prevision, or lack of it, did Rumford appear to have of the 
important discoveries about energy made near the middle of the nineteenth 
century? In answering, consider,, among other things, his comment (p. 186) 
that heat for cooking food might be produced by employing a horse coupled 
with a suitable mechanical contrivance, but that it might better be obtained 
by using the horse's fodder as fuel. 

60. Would the value for the mechanical equivalent of heat computed on 
page 92 have been larger or smaller if Rumford's data for experiment No. 3 
had included estimates of: (a) the heat absorbed by the wooden box; (b) 
the heat lost to the atmosphere; (V) the mechanical work done against fric- 
tional forces in the mechanism connecting the horse to the cannon? 

61. In so far as you can judge from the present paper, do you agree or 
disagree with the assertion that Rumford was unaware of the significance 
and importance of the quantity that in later years came to be called the 
mechanical equivalent of heat? Cite evidence for your conclusions. 

62. It has been asserted that Rumford was able to conclude from these 
experiments that the quantity of heat developed was (i) directly proportional 
to the work done and (ii) had no relation to the weight of the chips or dust. 


(a) Examine the accuracy of these assertions; include in your examination 
an analysis of the data of experiment No. 3. () Discuss the significance and 
relative importance of conclusions (i) and (ii) in the light of subsequent 
developments in thermal science. 

63. In 1871 a prominent scientist expressed the opinion that Rumford's 
cannon-boring experiment annihilated the material, or caloric, theory of 
heat. Do you agree or disagree, and why? 

64. Cite evidence to show whether or not Rumford, in his present work 
on heat, should be characterized as (a) a good strategist; (b) a good tacti- 
cian, (c] How do Rumford and Black compare in these respects? 

65 A.. In the specific-heat experiments (p. 172), why was it advantageous to 
use "thin slips separated from the ... block of metal by means of a fine 

66A. On page 173, Rumford says that the "4590 grains of water" included 
an allowance for the heat capacity of the "tin vessel." Supposing that he 
actually used 4380 grains of water and that the vessel weighed 0.30 Ib, show 
that the specific heat of the "tin" must have been Btu/lb F. 

67A. By using the cooling data given in Table i, estimate what the tem- 
perature of the cylinder probably would have been at the end of 30 min of 
operation if the quantity of heat lost from cylinder to surroundings could 
have been reduced to a negligibly small amount. 

68 A. On page 184, it is asserted that the quantity of heat needed to raise 
the temperature of 36.75 in. 3 of iron from 60 to 2ioF was 182 Btu. Show 
that one can obtain this value by assuming that the specific heat and density 
of the iron were 0.115 ^ tu /lb F and 496 lb/ft 3 , respectively, these being 
approximately the modern values for these two quantities. 

6pA. John Robison's Steam and Steam Engines (1818), vol. II, p. 145, 
quotes James Watt as saying, in part, that "A horse going at the rate of 2f 
miles an hour raises a weight of 150 pounds by a rope passing over a 
pulley." Show that these figures yield the value 33,000 ft Ib/min, or 550 ft 
Ib/sec, for the power of a horse. 

70 A. (a) Show that the value for the mechanical equivalent of heat com- 
puted on page 200 from Rurnford's data differs by 28 percent from the value 
accepted today, (b) J. P. Joule, from the results of a series of experiments of 
various types, concluded in 1850 that 772 ft Ib/Btu was the best value for the 
mechanical equivalent of heat that he had obtained up to that time. How 
much does this value differ from the accepted value? 

7 1 A, In what ways might Rumford have improved his apparatus and 
methods if he had recognized the importance of trying to find an accurate 
and unvarying quantitative relation between heat and mechanical work? 

72A. Sadi Carnot, a brilliant scientist of tremendously great promise who 
died of cholera during an epidemic in 1832, when he was only 36 years old, 
made a surprisingly accurate determination of the mechanical equivalent of 
heat, but this fact remained unknown until 1872, when some of his notes 
were published posthumously. If you had to help decide the question 
whether Carnot should be acclaimed as the "real discoverer of the mechani- 

210 CASE 3 

cal equivalent of heat," what factors or kinds of information would you try 
to take into account in reaching a decision? 

5. Humphry Davy's early wor\ on the production of heat by friction 

73. In modern science the term power denotes the physical quantity 
"mechanical work done per unit time." In what sense does Davy use 
"power" an pages 190 and 192? 

74. What was the temperaturt of the atmosphere during experiment II? 

75. From the data on page 193 one can show that 0.5 Ib of ice was used 
in experiment II. (a) Show that 74 Btu of heat would be needed to change 
this ice, which was initially at 29?, into water at 35F. () If it had been 
true, as Davy thought, that no appreciable part of this heat was supplied by 
thermal conduction from the surroundings, how much mechanical work 
would he have done on the ice to produce the heat? (Recall that i Btu is 
equivalent to 777.9 ft Ib.) 

76. For each of Davy's two experiments, state: (a) the hypotheses and 
deductions that led him to make the experiment; (&) the factors that he 
considered relevant in planning it; (r) other factors that he might have 
considered relevant, and why he may have ignored them; (d) the factors 
that he tried to keep constant and the variables that he observed or meas- 
ured; (e) the conclusions. 

77. In experiment III, suppose that Davy possibly by continuing the 
operation for a longer time had succeeded in producing a much larger 
quantity of heat, so that, if it were freezing water in the channel that was 
furnishing this heat, the new ice thus produced would have been clearly 
visible. If, under these circumstances, he had not observed new ice, would he 
have had an ironclad case for his contentions that the heat evolved did not 
come from either the water, the ice, or the outside bodies in contact with 
the ice, and therefore that caloric does not exist? (Before trying to answer 
this question, it might be well to make a brief outline of Davy's whole 

78. Comment critically on the following statements, which appear in va- 
rious books published since 1930: (i) "Davy's ingenious experimental pro- 
cedure was to rub two pieces of ice together in the absence of air." (ii) 
"Davy rubbed pieces of ice together in air, and then in a vacuum." (iii) 
"Davy found that the rate of melting of the ice was proportional to the 
mechanical work done in rubbing the ice." (iv) "The idea of trying to pro- 
duce heat by means of ice was novel, and has naturally elicited admiration; 
some historians consequently may have been tempted to give young Davy 
more credit in this connection than is due him." (v) "Rumford's conclusion 
in his paper on the boring of cannon was vigorously attacked by the calorists, 
but it was thoroughly confirmed in 1799 by Davy." 

79. In referring to this essay of Davy's, a recent writer says that nine- 
tenths of it are ingenuous and fallacious speculation, but one-tenth shows 
the high genius of this young man of 19 years who was soon to enter on a 


brilliant career in physical science. Do you find any evidence in the present 
excerpts to substantiate either of these assertions? 

80. Why is it that most people even those who are familiar with the 
modern, energy theory of heat still find it useful to employ the ideas and 
terminology of the material theory in describing or thinking about thermal 
processes in which the heat is conserved that is, not transformed into 
other forms of energy during the process? 

81. It has been said that a certain degree of healthy ignorance is an 
asset to a research worker. Suggest reasons why this may be true. 

82. Michelangelo, the most famous of the Florentine artists of the Ren- 
aissance, once said: "I criticize not by finding fault but by a new creation." 
Referring to the realm of the sciences, J. B. Conant, in "The Overthrow of 
the Phlogiston Theory" (Case 2, Harvard Case Histories in Experimental 
Science), says: "The overthrow of the phlogiston theory involved the de- 
velopment of a superior conceptual scheme." (a) Discuss the implications 
of these two comments, with special reference to the effectiveness of the meth- 
ods of attack on the caloric theory employed by Rumford (Sees. 3 and 4) and 
Davy, (b) Is there much evidence that Rumford and Davy were influenced 
in their choice of experiments and ways of reasoning about them by the 
fact that they were working in opposition to current scientific beliefs about 
the nature of heat? 

83. In a paper entitled "Recherches sur le Pr ogres lent du Melange 
spontane de certains Liquides. . ." (1807), Rumford described experiments 
which indicated that the particles of a liquid are in motion even when all 
parts of the liquid are at the same temperature. In what essential way does 
this this mode of attack on the caloric theory differ from those employed by 
Rumford and Davy in the experiments described in Sections 3, 4, and 5? 

84 A. Compute the weight of the ice used in experiment II. 

85 A. In connection with experiment III, show that : (a) the total quan- 
tity of heat needed to warm 0.5 Ib of iron through iF and at the same 
time to melt 18 grains of beeswax (heat of fusion, 2 Btu/lb) is 0.06 Btu; (b) 
the heat evolved when about 3 grains of water at ^2F changes to ice at 
32F is 0.06 Btu. 

86A. Compute the volume of 3 grains of ice. 

8yA. An experiment that Rumford or Davy could have performed., if it 
had occurred to them, is to stir, or churn, a liquid such as water and ob- 
serve whether it rises in temperature. As a way to attack the caloric theory, 
how does this experiment compare with those involving either abrasion or 

88A. It has been said that we tend to characterize a phenomenon as 
"anomalous" as long as we are unable to fit it into the conceptual scheme 
that we employ for describing other related phenomena. (^) Can you cite 
examples from your own experiences that seem to substantiate this asser- 
tion? (b) Do these examples furnish any indication that you may need to 
enlarge or revise certain of your conceptual schemes? (c) Does the way in 
which water expands and contracts with changes in temperature (p. 83) 
appear to be anomalous when viewed in the light of the caloric theory? 


(The asterisks indicate references that should 
be especially helpful to the beginner.) 

General references 

*i. C. B. Boyer, "History of the measurement of heat," Scientific 
Monthly, vol. 57 (1943), pp. 44 2 ~45 2 > 54 6 ~554- 

*2. }. B. Conant, On Understanding Science An Historical Approach 
(Yale University Press, 1947). The underlying philosophy of the case-his- 
tory method, and some important educational objectives that may be reached 
through it, 

*3. W. F. Magie, A Source Eoo\ in Physics (McGraw-Hill, 1935). 

4. E. Mach, Die Principien der Wdrmelehre (Barth, 1919). A critical 
and historical presentation of the whole subject of heat. 

5. R. M. Button (editor), Demonstration Experiments in Physics (Mc- 
Graw-Hill, 1938). The section on "Heat," pp. 193-248, describes 182 
demonstration experiments, many of which can be used to show the phe- 
nomena and experiments discussed or mentioned in the present case history. 

*6. L. W. Taylor, Physics -The Pioneer Science (Houghton Mifflin, 
1941). A first-year college textbook of physics, written from the historical 
point of view. 

*y. A. Wolf, A History of Science, Technology and Philosophy in the 
i6th and ijth Centuries (Macmillan, 1935). 

*8. A. Wolf, A History of Science, Technology and Philosophy in the 
1 8th Century (Macmillan, 1939). 

Evolution of the thermometer 

9. H. C. Bolton, Evolution of the Thermometer (Chemical Publishing 
Co., 1900). A brief history; it should be supplemented with the more recent 
references n, 12, 13, 16, and 17. 
*io. C. B. Boyer, reference i, pp. 442-447. 

11. C. B. Boyer, "Early principles in the calibration of thermometers," 
American Journal of Physics, vol. 10 (1942), p. 176. The history of the "one- 
fixed-point" and the "two-fixed-points" methods of calibration. 

12. N. E. Dorsey, "Fahrenheit and Roemer," Journal of the Washington 
Academy of Science, vol. 36 (1946), pp. 361372; for a digest of parts of 
this article, see I. B. Cohen, his, vol. 39 (1948), pp. 5658. 

13. J. N. Friend, "The origin of Fahrenheit's thermometric scale," 
Nature, vol. 139 (1937), pp. 395, 586. 

14. W. J. Lyons, "Inaccuracies in the textbook discussions of the ordinary 
gas laws," American Journal of Physics, vol. 6 (1938), p. 256. 

*i5. W. F. Magie, reference 3, pp. 125-133. Excerpts from papers by 
Newton, Amontons, and Fahrenheit. 


1 6. K. Meyer, "Ok Romer and the thermometer/' Nature, vol. 82 ( 1910), 
pp. 296-298; vol. 139 (1937), pp. 585-586. 

17. F. S. Taylor, "The origin of the thermometer/' Annals of Science, 
vol. 5 (1942), pp. 129-156. 
*i8. L. W. Taylor, reference 6, pp. 249-255. 
^19. A. Wolf, reference 7, pp. 82-91. 
*20. A. Wolf, reference 8 3 pp. 306-312. 

Joseph Blac\; early theories of heat 

21. F. Allen, "Newton on heat as a mode of motion," Science, vol. 99 
(1944), p. 299. 
*22. C. B. Boyer, reference i, pp. 447-452. 

23. J. Black, Lectures on the Elements of Chemistry, revised and pre- 
pared for publication by John Robison (Edinburgh, 1803), vol. i. Robison's 
preface contains a biography of Black. 

24. S. C. Brown, "The caloric theory of heat," American Journal of 
Physics, vol. 18 (1950). 

25. H. W. Dickinson and H. P. Vowles, James Watt and the Industrial 
Revolution (Published for the British Council by Longmans, Green, 1943; 
new ed., 1948). 

26. D. G. Fahrenheit, Philosophical Transactions, vol. 33 (1724), p. 78. 
Undercooling of water. 

^27. L B. Hart, James Watt and the History of Steam Power (Schuman, 
1949). An excellent popular account; good diagrams. 

28. D. McKie and N. H. deV. Heathcote, The Discovery of Specific and 
Latent Heats (Arnold, 1935). A careful, critical study of the work of Black 
and his contemporaries, notably Wilcke. 

^29. W. Ramsey, The Life and Letters of Joseph Blac\ (Constable, 1918). 
30. H. L. Smith, "The origin of the horsepower unit," American Jour- 
nal of Physics, vol. 4 (1936), pp. 120-122. 
*3i. L. W. Taylor, reference 6, pp. 264-269, 279-285. 
32. E. C. Watson, "Portraits and caricatures of Joseph Black, and prints 
of Edinburgh and Glasgow in his day/' American Journal of Physics, vol. 

^33. A. Wolf, reference 8, pp. 177-183. 

Count Rumford 

^34. C. B. Boyer, reference i, pp. 548-550. 

*35. S. C. Brown, "The discovery of convection currents by Benjamin 
Thompson, Count of Rumford," American Journal of Physics, vol. 15 (1947), 
pp. 273-274. 

36. S. C. Brown, "Count Rumford and the caloric theory of heat/* 
Proceedings of the American Philosophical Society, vol. 93 (1949), pp. 
316-325. An excellent review of Rumford's various experiments, extending 
over a 30-year period, in which he attacked the caloric theory from many 
different points of view, 

214 CASE 3 

37. G. E. Ellis, Memoir of Sir Benjamin Thomptvson, Count Rumford 
(Macmillan, 1876). A biography. 

38. G. Fordyce, Philosophical Transactions, vol. 75 (1785), p. 361. 
Fordyce's own account of his experiments on the weight of heat. 

^39. W. F. Magie, reference 3, pp. 146-151. An excerpt from Rumford's 
essay, "On the propagation of heat in fluids" (1797), in which he describes 
his discovery of the convection of heat. 

40. D. McKie and N. H. deV. Heathcote, reference 28, pp. 137-148. 

*4i. M. S. Powell, "Count Rumford, soldier, statesman, scientist," 
American Journal of Physics, vol. 3 (1935), pp. 161-167. A biography. 

^42. L. W. Taylor, reference 6, chap. 22. 

43. }. A. Thompson, Count Rumford of Massachusetts (Farrar & Rine- 
hart, 1935). Concerned chiefly with Rumford's nonscientific activities. 

44. A. Tilloch, Philosophical Magazine, vol. 9 (1801), p. 158. Criticisms 
of the various experiments on the weight of heat. 

^45. A. Wolf, reference 8, pp. 193-198. 

46. The Complete Worths of Count Rumford (American Academy of 
Arts and Sciences, 1870-75). 4 vols. Volume 4 contains an extensive bibliog- 
raphy of works by or on Rumford. 

47. Rumford's Complete Worths (Macmillan, 1876). 5 vols. 

Sir Humphry Davy 

48. E. N. da C. Andrade, "Humphry Davy's experiments on the fric- 
tional development of heat," Nature, vol. 135 (1935), pp. 359-360. 

*49- J. G. Crowther, Men of Science (Norton, 1936), pp. 366. A biog- 

50. J. Davy (editor), The Collected Worfys of Sir Humphry Davy 
(London, 1839), vol. 2, pp. 986. 

'Early history of the energy concept and principle of conservation of energy 

51. A. E. Bell, "The concept of energy," Nature, vol. 151 (1943), pp. 

*52. C. B. Boyer, reference i, pp. 546-554. 

53. P. S. Epstein, Textboo^ of Thermodynamics (Wiley, 1937), pp. 

2 7-34- 

54. E. Mach, History and Root of the Principle of the Conservation of 
Energy (Open Court, 1911). 

55. W. F. Magie, reference 3, pp. 59-60, 197-220. Excerpts from papers 
by Young, Mayer, Joule, and Helmholtz. 

56. A. Wood, Joule and the Study of Energy (Bell, 1925). 


The Atomic -Molecular 





The Theory 


Some of the earliest writings that have come down to us from 
ancient civilizations display a recurrent speculation about the ultimate 
character of matter. Are the materials presented to us by nature, and 
those produced by art, capable of subdivision without limit; or do they 
consist of certain extremely minute particles (atoms) which cannot be 
further subdivided without destruction of the identity of the material? 
Almost 2500 years ago the Greek philosophers Leucippus and Democ- 
ritus propounded a fairly clear and persuasive formulation of the 
atomistic point of view. Prescient as it appears to us, their view was 
primarily a speculative response to certain everyday observations of 
nature. This response was conditioned by certain apparent logical para- 
doxes connected with the idea that matter is infinitely subdivisible; and 
the scientific development of the early Greeks was entirely inadequate 
for the basic resolution of such a weighty issue on experimental 
grounds. Such a towering speculative structure erected on so small a 
base of common observations could be, and was, opposed by other phi- 
losophies similarly based, but differently constructed. Thus the atomic 
hypothesis, together with the relatively materialistic world view with 
which it was at first associated, was controverted by other philosophers, 
notably by Aristotle. However, the original question was still entirely 
unresolved, and discussion of it continued, more or less actively, for 
some 2000 years. Only toward the close of the eighteenth century had 
scientific development achieved a sufficient degree of sophistication to 
permit a fruitful reexamination of the entire problem. 

By the time of the Late Renaissance, with its notable quickening of 
interest in experimental science, the original writings of Leucippus and 
Democritus had been lost, and the learned world was acquainted with 
their opinions only through the animadversions of other philosophers 
and, somewhat more directly, through the didactic poem "De Rerum 
Natura" in which Lucretius (98-55 B.C.) provided an exposition and an 
enthusiastic appraisal of some aspects of Greek atomism. However, 
many of the foremost natural philosophers of this era seriously enter- 
tained one or another form of the atomistic viewpoint. Furthermore, 
with the gradual decay of the akhemistic contention that different 

218 CASE 4 

kinds of matter could be converted into one another, the permanence 
and immutability of the atoms characteristic of different materials be- 
came more plausible. There resulted a vigorous revival of the atomistic 
viewpoint so much so that toward the middle of the eighteenth cen- 
tury we find Voltaire writing: "Atoms are accepted, indivisible, and 
immutable principles to which is due the changelessness of the differ- 
ent elements and the different kinds of bodies." 

The more widespread credence accorded the atomistic hypothesis 
arose not from any new direct evidence for its "correctness" but, at least 
in part, because it was found to provide an extraordinarily useful way 
of thinking about nature, helping to construe natural phenomena in 
terms of mechanical models and analogies. This usefulness was much 
extended after the completion of the chemical revolution initiated by 
Lavoisier (1743-1794)? when clarification of the concept of chemical 
elements helped foster the idea that these elements consisted of certain 
characteristic kinds of atoms. It is perhaps significant that one of the 
first statements of a detailed atomic hypothesis, in a form approximat- 
ing that which still prevails, was made in 1789 in a work on A Com- 
parative View of the Phlogistic and Antiphlogistic Theories, written 
by William Higgins (1766-1835) in support of the new oxygen theory 
of Lavoisier. 

Although, up to this time, the atomistic hypothesis had found an 
ever-widening usefulness in "explaining" or "understanding" natural 
phenomena, it still remained a speculative idea. Not only was it most 
tenuously supported by experimental evidence, but it had not been 
applied in a single definite form to the correlation of a wide variety of 
phenomena and, most important of all, it had not yet exercised the 
highest function o a new conceptual scheme the suggestion of new 
experiments. With Higgins's publication we see the beginning of the 
transmutation of this speculative idea. Indeed, before the passage of 
another score of years this extremely ancient notion had been placed 
before the learned world in the character of a well-developed conceptual 
scheme that was found to "explain" a great many of the previously dis- 
covered data of chemistry and physics, and that was fruitful of .numer- 
ous new ideas and experiments. How this metamorphosis was accom- 
plished is the subject of the present work. 

In Section i we shall view the deceptively simple proposals advanced 
by John Dalton (1766-1844), the effective architect of the atomic theory 
as we know it today. Dalton, the son of a poor Quaker weaver, received 
little formal education but was himself a teacher in a village school 
when he was no more that twelve years old. He spent most of his life 
in Manchester, where he was for a time an instructor in various 
branches of natural philosophy at the New College, and later a free- 


lance tutor in these subjects. Despite his meager training, Dalton dis- 
played considerable scientific acumen in the development of his atomic 
theory. He presented a clear and concrete formulation of the funda- 
mental postulates on which a meaningful atomic theory could be 
founded. With the aid of a bold assumption he achieved a drastic 
simplification of an extraordinarily complex situation. Finally, lacking 
the means of securing direct evidence for his conception he showed in 
a masterly way how indirect evidence for this essentially physical 
hypothesis could be developed from chemical data that were fairly 
readily obtainable. 

In Section 2 we shall observe the striking and immediate achieve- 
ments of the atomic theory in relation to the then contemporary chem- 
istry. There were few who were not favorably impressed by those 
achievements, but there were, then and later, many who admitted that 
matter behaved as though it were composed of Daltonian atoms but 
who nevertheless maintained a skeptical attitude toward the postulated 
real existence of these atoms. In particular, there were many who felt 
considerable doubt about the validity of the basic simplifying assump- 
tion with the aid of which the atomic theory had originally been 
brought to bear upon chemical phenomena; indeed, to some slight 
extent, Dalton shared their doubts. The support of this assumption, or 
the substitution for it of some more prepossessing alternative, was cor- 
rectly recognized as one of the pivotal factors that would determine 
the future usefulness of the atomic theory. 

In Section 3 we shall follow the discovery, by Joseph Louis Gay- 
Lussac (1778-1850), of an empirical relation that ultimately suggested 
the desired better substitute for Dalton's assumption. Gay-Lussac, a 
superb experimentalist, was a product of the Ecole Polytechnique. In 
the course of his distinguished career he made a large number of 
fundamental contributions to both pure science and industrial tech- 
nology and, in his later years, to the organization of scientific projects 
of interest to his government. 

In Section 4 we shall examine Dalton's rejection of Gay-Lussac's im- 
portant work. Although this work ultimately led to a vital complement 
to Dalton's original theory, Dalton's rejection of it was based on reason- 
able grounds. The new relation appeared to be in fundamental contra- 
diction with certain tenets that seemed to him essential to the atomic 
theory as such. 

In Section 5 we shall see how Amadeo Avogadro di Quaregna (1776- 
1856) penetrated to the heart of this apparent anomaly and showed the 
way in which it might be dissipated. Avogadro was born in Turin and 
educated at its University, where he later occupied the chair of mathe- 
matical physics. In the important paper that has made his fame secure 

220 CASE 4 

Avogadro succeeded not only in providing a reconciliation of appar- 
ently incompatible viewpoints, but, in so doing, he also indicated how 
the empirical relations established by Gay-Lussac could lead to a much 
less arbitrary supposition than the rather dubious assumption that 
Dalton had found it necessary to use. With Avogadro's proposal the 
framework of the modern atomic-molecular theory was essentially 
completed less than five years after the publication of the first out- 
line of Dalton's new conceptual scheme. 

A major advance achieved with such rapidity inspires our respect. 
We cannot distinguish all the factors that contributed to the speed of 
this development. Surely not the least important of these factors was 
the possession by Dalton, and several of his contemporaries, of a most 
penetrating scientific intuition or, more precisely, a genius for forg- 
ing ahead by guessing right when insufficient criteria were available 
to support a completely reasoned judgment. However, the speed char- 
acterizing the initial growth of the atomic-molecular theory is super- 
ficially no more remarkable than the delay of approximately 50 years 
that intervened before the essential correctness of Avogadro's synthesis 
was fully recognized by the scientific world. Fascinating as it is, the 
complete story of this 50-year lag is so involved as to lie beyond the 
compass of the present work. 

In Section 6, then, we shall only indicate some of the unavoidable 
weaknesses in Avogadro's position that, in one form or another, so long 
delayed the acceptance of his views. Finally, a sketch of the steps leading 
up to this eventual acceptance will conclude the present study. 


Dalton's Approach to the Atomic Theory. The tradition of 
atomism, used as a qualitative way of thinking about natural phe- 
nomena, was quite strong in English scientific history, and is well dis- 
played in the many works of Bacon, Boyle, Hooke, and Newton. 
Dalton, a fervent admirer of Newton, was thus thoroughly imbued 
with this heritage of atomism. Moreover, Newton's striking success in 
interpreting a large number of terrestrial and celestial phenomena in 
terms of the action of finite forces between real bodies naturally en- 
couraged attempts to construe other phenomena in like fashion. Dal- 
ton's position was further a privileged one in that he worked at a period 
when the long, slow development of "pneumatic chemistry," culminat- 
ing in the work of Cavendish, Priestley, and Lavoisier, finally made it 
possible to approach the atomic theory by the route through which it 
was most readily accessible, namely, the study of gases. Evidence that 
the time was, indeed, ripe is seen in the fact that the fruitful line 


adopted by Dalton had been missed by William Higgins in 1789 by a 
margin so narrow that Higgins's claim to priority was for some time 
maintained by Davy, who, however, subsequently foreswore this con- 
tention. Thus it appears that Dalton labored at a time when, and in a 
milieu from which, the development of a realistic atomic theory could 
not have been too long postponed. 

The sequence of events by which Dalton arrived at his celebrated 
theory is regrettably obscure, particularly since Dalton himself has 
given us several different accounts. A judgment on the basis of his 
published papers is rendered difficult by a curious situation reminiscent 
of that attending the publications of Lavoisier on combustion. The 
papers, read in 1802 and 1803, in which Dalton appears to be grappling 
with the problems of the atomic theory were not published until 1805, 
when they appeared in the Memoirs of the Literary and Philosophical 
Society of Manchester. A study of Dalton's notebooks has indicated 
that some of the experiments presumably discussed in the paper read 
in 1803 were actually not performed until 1804. Thus Dalton apparently 
brought his paper up to date at the time of its publication in 1805; he 
had ample opportunity for such revision since he was the secretary of 
the Society at that time. Consequently, it is very difficult for us to decide 
what represents his original conception and what is the result of subse- 
quent elaboration. A careful examination of the available indications 
leads to the conclusion that Dalton's earliest intimations of his atomic 
theory came to him from studies undertaken in connection with his 
lifelong interest in meteorology. It seems probable that through his 
purely physical investigations of the behavior of mixtures of gases and 
of the solubility of gases in liquids (the phenomena here involved are 
not, in fact, highly relevant to the atomic theory) he was led from a 
philosophical Newtonian atomism to a concrete apprehension of the 
methods whereby an atomic theory might be supported by chemical 
experiments. The excerpts printed below are particularly valuable in 
showing how this approach encouraged Dalton to believe that there 
were significant differences in the sizes of the particles of various gases. 
This belief had a most important influence on the further development 
of the atomic theory, in that it disposed Dalton to discount subsequent 
discoveries that provided a vital supplement to his original theory. 

The following excerpt, containing Dalton's first announcement of 
his atomic theory, is the concluding section of a paper "read before a 
select audience of nine members and friends in the rooms of the Literary 
and Philosophical Society of Manchester on 2ist October 1803." The 
subject of this paper is "On the Absorption of Gases by Water and 
Other Liquids," and the fact that the announcement occurs in this 
context provides a strong indication that Dalton's original conception 

222 CASE 4 

of his chemical atomic theory grew out of his studies of phenomena in 
which chemical reactions are scarcely involved. In the final section, 
dealing with the "Theory of the Absorption of Gases by Water," 
Dalton remarks: 

The greatest difficulty attending the mechanical hypothesis, arises 
from different gases observing different laws. Why does water not admit 
its bulk of every kind of gas alike? [i.e., why are not all gases equally 
soluble in water?] This question I have duly considered, and though I 
am not yet able to satisfy myself completely, I am nearly persuaded that 
the circumstance depends upon the weight and number of the ultimate 
particles of the several gases: Those whose particles are lightest and single 
being least absorbable, and the others more according as they increase 
in weight and complexity. (Subsequent experience renders this conjec- 
ture less probable.) An enquiry into the relative weights of the ultimate 
particles of bodies is a subject, as far as I know, entirely new: I have 
lately been prosecuting this enquiry with remarkable success. The prin- 
ciple cannot be entered upon in this paper; but I shall just subjoin the 
results, as far as they appear to be ascertained by my experiments. 

Dalton here appends a "Table of the relative weights of the ultimate 
particles of the gaseous and other bodies." This is the first published 
tabulation of atomic weights, and the figures cited make it plain that 
Dalton had by this time formulated all the essential parts of his theory. 

A fuller account of Dalton's progress toward the atomic theory has 
been found in his manuscript notes for one of a series of lectures which 
he delivered early in 1810 at the Royal Institution (founded in 1799 at 
the instance of Count Rumford) . The notes here reproduced were for 
the seventeenth lecture of the series, and it is interesting to observe that 
this discussion followed directly after two lectures on heat. Dalton's 
ideas about heat seem to have played an important role in the develop- 
ment of his theory, and he states that "the doctrine of heat is justly con- 
sidered as constituting an essential part of chemical science/' Although 
Dalton was familiar with the dynamical theory of heat which related 
heat to the motion of submicroscopic particles the "doctrine of heat" 
that he adopted in the construction of his atomic theory considers heat 
as a tangible substance which is weightless, or of negligible weight. 

As the ensuing lectures on the subject of chemical elements and their 
combinations will perhaps be thought by many to possess a good deal 
of novelty, as well as importance, it may be proper to give a brief histor- 
ical sketch of the train of thought and experience which led me to the 
conclusions about to be detailed. 

Having been long accustomed to make meteorological observations, 
and to speculate upon the nature and constitution of the atmosphere, it 
often struck me with wonder how a compound atmosphere, or a mixture 


of two or more elastic fluids, should constitute apparently a homogeneous 
mass, or one in all mechanical relations agreeing with a simple atmos- 
phere. [Dalton had published, in 1793, a book on meteorology in which 
there is some faint foreshadowing of a concern with the problem to 
which he directs our attention. "Compound" is used here not in the 
sense of chemical combination, but merely to distinguish a mixed atmos- 
phere from a simple one-component atmosphere.] 

Newton has demonstrated clearly, in the 23rd Prop, of Book 2 of the 
Prindpia, that an elastic fluid is constituted of small particles or atoms 
of matter, which repel each other by a force increasing in proportion as 
their distance diminishes. 1 But modern discoveries having ascertained 
that the atmosphere contains three or more elastic fluids, of different 
specific gravities, it did not appear to me how this proposition of Newton 
would apply to a case of which he, of course, could have no idea. 

The same difficulty occurred to Dr. Priestley, who discovered this 
compound nature of the atmosphere. He could not conceive why the 
oxygen gas, being specifically heaviest, should not form a distinct 
stratum of air at the bottom of the atmosphere, and the azotic gas one 
at the top of the atmosphere. [In conformity with the usage of his day, 
Dalton employs "azotic gas" or "azote" to signify nitrogen. The form 
survives in modern French.] Some chemists upon the Continent, I be- 
lieve the French, found a solution of this difficulty (as they apprehended). 
It was chemical affinity [an attraction or tendency that was believed to 
cause substances to combine, react, or form solutions with one another]. 
One species of gas was held in solution by the other; and this compound 
in its turn dissolved water; hence evaporation, rain> etc. This opinion of 
air dissolving water had long before been the prevailing one, and natu- 
rally paved the way for the reception of that which followed, of one kind 
of air dissolving another. It was objected that there were no decisive 
mar\s of chemical union, when one kind of air was mixed with another. 
The answer was, that the affinity was of a very slight kind, not of that 
energetic cast that is observable in most other cases. [That is, since there 
is no readily observed change of volume or temperature when the 
separated atmospheric gases are mixed, it Is hypothesized that their 

x lf Dalton merits the title of "father of the atomic theory/' we must allow Newton 
the position of "grandfather" of the theory. This is true not only because of his profound 
influence on Dalton, as here displayed; but even more important, because thousands of 
years after the earliest thought of an atomic theory, he was the first to assess the value 
of this concept by quantitatively measuring it against experience. Thus, in the Proposition 
to which Dalton refers, Newton demonstrates that: 

"A ... gas which is made up of mutually repulsive particles ... the forces be- 
tween which are reciprocally proportional to the distances between their centres, will 
make up an elastic fluid, the density of which is proportional to the pressure ..." (i.e., 
an clastic fluid that obeys Boyle's Law). 

It is interesting to observe that Dalton has misrepresented the content of Newton's 
demonstration, which proved only that if such an hypothesis were accepted, Boyle*s Law 
could be "explained," but which did not prove, as Dalton suggests, that such an hypothe- 
sis is the only possible explanation of Boyle's Law. Indeed, the modern explanation is 
essentially different from that proposed by Newton. 

224 CASE 4 

tendency to react (i.e., their affinity) is weaker than in the normal 
chemical processes, where there are usually fairly obvious indications 
of the progress of the reaction.] 

I may add, by-the-bye, that this is now, or has been till lately, I believe, 
the prevailing doctrine in most of the chemical schools in Europe. 

In order to reconcile or rather adapt this chemical theory of the atmos- 
phere to the Newtonian doctrine of repulsive atoms or particles, I set to 
work to combine my atoms upon paper. I took an atom of water, another 
of oxygen, and another of azote, brought them together, and threw 
around them an atmosphere of heat ... I repeated the operation, but 
soon found that the watery particles were exhausted (for they make but 
a small part of the atmosphere). [The weight and volume percentages 
of nitrogen, oxygen and water vapor in the atmosphere were known in 
Dalton's time. Dalton speaks here in terms of the relative numbers of 
the ultimate particles of these components, which he probably calculated 
from the proportions by volume with the aid of the "confused idea" 
(see page 267) that equal volumes of different gases contain equal num- 
bers of their respective particles. Such a calculation indicates that for 
each particle of water vapor there are about 20 particles of oxygen, and 
some 80 azotic particles.] I next combined my atoms of oxygen and azote, 
one to one; but I found in time my oxygen failed; I then threw all the 
remaining particles of azote into the mixture, and began to consider 
how the general equilibrium was to be obtained. [This combination and 
manipulation of atoms "upon paper" refers to an entirely hypothetical 
situation, or "thought experiment," by which Dalton proposed to dis- 
cover the bearing of the atomic theory on the problem of the homo- 
geneity of a "compound" atmosphere.] 

My triple compounds of water, oxygen, and azote were wonderfully 
inclined, by their superior gravity, to descend and take the lowest place; 
the double compounds of oxygen and azote affected to take a middle 
station; and the azote was inclined to swim at the top. I remedied this 
defect by lengthening the wings of my heavy particles, that is, by throw- 
ing more heat around them, by means of which I could make them float 
in any part of the vessel; but this change unfortunately made the whole 
mixture of the same specific gravity as azotic gas this circumstance 
could not for a moment be tolerated. In short, I was obliged to abandon 
the hypothesis of the chemical constitution of the atmosphere altogether, 
as irreconcilable to the phenomena. 

A better grasp of Dalton's conception of the heat "atmosphere" 
around his ultimate particles can be secured from the following excerpt 
from his short manuscript article "On Heat,'* dated May 23, 1806: "Ac- 
cording to this view of the subject, every atom has an atmosphere of 
heat around it, in the same manner as the earth or any other planet has 
its atmosphere of air surrounding it, which cannot certainly be said to 
be held by chemical affinity, but by a species of attraction of a very 


different kind. Every species of atoms or ultimate particles of bodies 
will be found to have their peculiar powers of attraction for heat, by 
which a greater or less quantity of that fluid will be conglomerated 
around them in like circumstances: this gives rise to what has been 
called the different capacities of bodies for heat or their specific heat. 
Any two bodies, the atoms of which have different capacities for heat, 
being placed in any medium will acquire the same temperature. This 
state consists in the several individual atmospheres of heat acquiring 
the same density at their exterior surface, or where they become con- 
tiguous. The virtual diameters of atoms of matter will therefore vary 
in like circumstances according to their attraction for heat; those with 
a strong attraction will collect a large and denser atmosphere around 
them, whilst those possessing a weaker attraction will have a less 
atmosphere, and consequently the virtual diameter, or that of the atom 
and its atmosphere together, will be less, though the atmospheres of 
both have precisely the same disposition to receive or to part with heat 
upon any change of temperature. . ." 

Thus by hypothesizing different attractions for heat, and heat shells 
of variable diameter, Dalton is able to vary the effective densities of his 
particles in much the same way that a fisherman adjusts the effective 
density of a lead sinker by attaching to it various quantities of cork. 
In attempting to adjust the particles of different weights so that all 
would have the same specific gravity he could not entirely remove the 
heat shell from the lightest particles (the nitrogen atoms) since he 
considered the heat shell to be the essential source of the repulsions by 
which the elastic (gaseous) state was maintained. Consequently he had 
no alternative but to extend the heat atmospheres around the heavier 
particles (i.e., to "lengthen their wings") until their specific gravity, 
and that of this chemically compounded atmosphere, were the same as 
for nitrogen a palpable contradiction of experience. 

There was but one alternative left, namely, to surround every individ- 
ual particle of water, of oxygen, and of azote, with heat, and to make 
them respectively centres of repulsion, the same in a mixed state as in a 
simple state. This hypothesis was equally pressed with difficulties; for, 
still my oxygen would take the lowest place, my azote the next, and my 
steam would swim upon the top. 

In 1801 I hit upon an hypothesis which completely obviated these 

According to this, we were to suppose that the atoms of one kind did 
not repel the atoms of another kind, but only those of their own kind. 
This hypothesis most effectually provided for the diffusion of any one 
gas through another, whatever might be their specific gravities, and 
perfectly reconciled any mixture of gases to the Newtonian theorem. 

226 CASE 4 

[According to this ingenious idea, stratification or segregation of particles 
of the same kind is prevented by strong, specific, mutual repulsions, 
which render any collection of particles of the same kind an unstable 
grouping. Consequently gases will mix with one another and will remain 
uniformly mixed despite differences in the intrinsic specific gravities of 
the components.] Every atom of both or all the gases in the mixture was 
the centre of repulsion to the proximate particles of its own kind, dis- 
regarding those of the other kind. All the gases united their efforts in 
counteracting the pressure of the atmosphere, or any other pressure that 
might be opposed to them. 

This hypothesis, however beautiful might be its application, had some 
improbable features. 

We were to suppose as many distinct \inds of repulsive powers, as of 
gases; and, moreover, to suppose that heat was not the repulsive power 
in any one case; positions certainly not very probable. Besides, I founo 
from a train of experiments which have been published in the Man- 
chester Memoirs, that the diffusion of gases through each other was a 
slow process, and appeared to be a work of considerable effort. 

Upon reconsidering this subject, it occurred to me that I had never 
contemplated the effect of difference of size in the particles of elastic 
fluids. By size I mean the hard particle at the centre and the atmosphere 
of heat taken together. If, for instance, there be not exactly the same 
number of atoms of oxygen in a given volume of air ["air" is used here, 
as by Priestley, as a generic term for "gas"] as of azote in the same vol- 
ume, then the sizes of the particles of oxygen must be different from 
those of azote. And if the sizes be different, then on the supposition that 
the repulsive power is heat, no equilibrium can be established by particles 
of unequal size pressing against each other . . . [Dalton's conclusion 
here is based on a rather abstruse (and erroneous) line of mechanical 
and geometrical reasoning which led him to believe that there would be 
no stratification of the components "the particles of one kind being 
from their size unable to apply properly to the other" at their common 
surfaces of contact.] 

This idea occurred to me in 1805. I soon found that the sizes of the 
particles of elastic fluids must be different. For a measure of azotic gas 
and one of oxygen, if chemically united, would make- nearly two meas- 
ures of nitrous gas, and those two could not have more atoms of nitrous 
gas than the one measure had of azote or oxygen. . ? Hence the sug- 

2 Dalton cites experimental data that appear to support his new viewpoint. Although 
the measurements of the combining volumes were relatively crude, they sufficed to show 
that, say, i cubic foot of oxygen would react with i cubic foot of nitrogen to form 
approximately 2 cubic feet of nitrous gas. Now if we assume that there are n atoms of 
oxygen in unit volume of oxygen, and n atoms of nitrogen in unit volume of nitrogen, 
we can form from them a maximum of n molecules of nitrous gas, each of which is com- 
posed of one atom of oxygen and one of nitrogen. But experiment showed that these 
molecules of nitrous gas occupied two unit volumes, implying that each volume of nitrous 
gas contained only l An molecules, or only half as many gaseous "particles" as were as- 
sumed to be present in unit volume of nitrogen or of oxygen. Dalton saw no alternative to 


gestion that all gases of different kinds have a difference in the size of 
their atoms; and thus we arrive at the reason for that diffusion of every 
gas through every other gas, without calling in any other repulsive 
power -than the well-known one of heat. [The compound gas is main- 
tained in a homogeneous condition through the mechanism referred to 
at the end of the immediately preceding paragraph.] 

This then is the present view which 1 have of the constitution of a 
mixture of elastic fluids. 

The different sizes of the particles of elastic fluids under like circum- 
stances of temperature and pressure being once established, it became an 
object to determine the relative sizes and weights, together with the 
relative number of atoms in a given volume. This led the way to the 
combinations of gases, and to the number of atoms entering into such 
combinations, the particulars of which will be detailed more at large in 
the sequel. Other bodies besides elastic fluids, namely liquids and solids, 
were subject to investigation, in consequence of their combining with 
elastic fluids. Thus a train of investigation was laid for determining the 
number and weight of all chemical elementary principles which enter 
into any sort of combination one with another. 

In these lecture notes of Dalton's three significant points should be 

(1) The successive consideration of ad hoc hypotheses, to discover 
one that adequately "explains" the experimental phenomena in terms 
of simple and plausible assumptions, is well exhibited. Such an ap- 
proach was and is of the greatest importance in scientific investigation. 

(2) Dalton's attention was focused on the sizes of his particles as 
well as on their weights, and he was led to believe that the same volume 
of different gases contained different numbers of "particles." This factor 
had a most important influence on the later history o the atomic theory. 

(3) But Dalton also calls attention to the importance of the weight 
relations of the ultimate particles, and it was in this connection that 
his theory proved most fruitful. 

(4) He has also stressed the view that chemical combination repre- 
sents an atom-to-atom linkage of small numbers of constituent bodies, 
rather than the physical solution of many particles of one kind in a 
multitude of particles of another kind. 

The Frameworl^ of the Atomic Theory. In the following passages 
are stated the fundamental postulates of the atomic theory. To facilitate 
comprehension of the content of these passages we may prefix them 
with an orthodox modern summary of the basic postulates. It is impor- 
tant to observe, however, that Dalton did not proceed in a clear-cut 

the conclusion that there were different numbers of particles in equal volumes of different 
gases. We shall soon see the unhappy consequences of this conclusion. 

228 CASE 4 

fashion from postulates to argument but that, rather, he followed a 
reverse course. The modern summary of his postulates might run: 

All matter is composed of atoms which are indivisible. 

All the atoms of a given element are alike in weight and in all other 

The atoms of different elements are of different weights. 

Atoms are indestructible and preserve their identities in all chemical 

The following passage is an excerpt from Dalton's notes for the 
eighteenth of the lectures that he gave at the Royal Institution, in 1810. 

We endeavoured to show that matter, though divisible in an extreme 
degree, is nevertheless not infinitely divisible. That there must be some 
point beyond which we cannot go in the division of matter. The exist- 
ence of these ultimate particles of matter can scarcely be doubted, though 
they are probably much too small ever to be exhibited by microscopic 

I have chosen the word atom to signify these ultimate particles, in 
preference to particle, molecule, or any other diminutive term, because I 
conceive it is much more expressive; it includes in itself the notion of 
indivisible, which the other terms do not. It may perhaps be said that I 
extend the application of it too far, when I speak of compound atoms-, 
for instance, I call an ultimate particle of carbonic acid a compound 
atom. Now, though this atom may be divided, yet it ceases to be carbonic 
acid, being resolved by such division into charcoal and oxygen. Hence I 
conceive there is no inconsistency in speaking of compound atoms, and 
that my meaning cannot be misunderstood. [The word "atom" derives 
from the Greek "atomos," signifying uncut or indivisible.] 

It has been imagined by some philosophers that all matter, however 
unlike, is probably the same thing; and that the great variety of its 
appearances arises from certain powers communicated to it, and from the 
variety of combinations and arrangements of which it is susceptible. 
From the notes I borrowed from Newton in the last lecture, this does 
not appear to have been his idea. Neither is it mine. I should apprehend 
there are a considerable number of what may be properly called elemen- 
tary principles, which never can be metamorphosed, one into another, 
by any power we can control. We ought, however, to avail ourselves of 
every means to reduce the number of bodies or principles of this appear- 
ance as much as possible; and after all we may not know what elements 
are absolutely indecomposable, and what are refractory, because we do 
not apply the proper means for their reduction. 

The next passages are taken from Dalton's A New System of 
Chemical Philosophy, the first part of which was published in 1808. 

Whether the ultimate particles of a body, such as water, are all alike, 


that is, of the same figure, weight, etc. is a question of some importance. 
From what is known, we have no reason to apprehend a diversity in 
these respects: if it does exist in water, it must equally exist in the ele- 
ments constituting water, namely, hydrogen and oxygen. Now it Is 
scarcely possible to conceive how the aggregates of dissimilar particles 
should be so uniformly the same. If some of the particles of water were 
heavier than others, if a parcel of the liquid on any occasion were con- 
stituted principally of these heavier particles, it must be supposed to affect 
the specific gravity of the mass, a circumstance not known. Similar ob- 
servations may be made on other substances. Therefore we may conclude 
that the ultimate particles of all homogeneous bodies are perfectly ali\e 
in weight, figure, &c. In other words, every particle of water is like 
every other particle of water; every particle of hydrogen is like every 
other particle of hydrogen. . . 

When any body exists in the elastic state, its ultimate particles are 
separated from each other to a much greater distance than in any other 
state; each particle occupies the centre of a comparatively large sphere, 
and supports its dignity by keeping all the rest, which by their gravity, 
or otherwise are disposed to encroach upon it, at a respectful distance. 
When we attempt to conceive the number of particles in an atmosphere, 
it is somewhat like attempting to conceive the number of stars in the 
universe; we are confounded with the thought. But if we limit the sub- 
ject, by taking a given volume of any gas, we seem persuaded that, let 
the divisions be ever so minute, the number of particles must be finite; 
just as in a given space of the universe, the number of stars and planets 
cannot be infinite. 

Chemical analysis and synthesis go no farther than to the separation 
of particles one from another, and to their reunion. No new creation or 
destruction of matter is within the reach of chemical agency. We might 
as well attempt to introduce a new planet into the solar system, or to 
annihilate one already in existence, as to create or destroy a particle of 
hydrogen. All the changes we can produce, consist in separating particles 
that are in a state of cohesion or combination, and joining those that were 
previously at a distance. 

In all chemical investigations, it has justly been considered an impor- 
tant object to ascertain the relative weights of the simples which con- 
stitute a compound. But unfortunately the enquiry has terminated here; 
whereas from the relative weights in the mass, the relative weights of the 
ultimate particles or atoms of the bodies might have been inferred, from 
which their number and weight in various other compounds would ap- 
pear, in order to assist and to guide future investigations, and to correct 
their results. Now it is one great object of this work, to show the impor- 
tance and advantage of ascertaining the relative weights of the ultimate 
particles, both of simple and compound bodies, the number of simple 
elementary particles which constitute one compound particle, and the 
number of less compound particles which enter into the formation of 
one more compound particle. 

230 CASE 4 

The Determination of the Relative Atomic Weights. The decks have 
now been cleared for action, and the calculation of the weights (rela- 
tive to hydrogen taken as i) of the ultimate particles defined above has 
been set as the goal. But, unfortunately, while the postulates already 
considered are essentially satisfactory and correct, they are not in them- 
selves sufficient to make possible a calculation of the atomic weights. 
A simple example will illustrate this point. 

The crude analyses used by Dalton indicated that about 6 grams of 
oxygen united with i gram of hydrogen to form 7 grams of water. 
Letting n represent the number of water molecules (or "compound 
atoms") so formed, then if the molecular formula of water is HO it is 
plain that n atoms of hydrogen weigh i gram while n atoms of oxygen 
weigh 6 grams; or one oxygen atom weighs six times as much as one 
hydrogen atom; or the atomic weight of oxygen, relative to hydrogen, 
is 6. However, if the formula of water is taken as HO 2 , n atoms of 
hydrogen will have reacted with 2n atoms of oxygen. Consequently, n 
atoms of oxygen weigh only 3 grams, and the weight of one oxygen 
atom relative to one hydrogen atom is then 3. In the same way, if the 
formula of water is assumed to be H 2 O, the atomic weight of oxygen 
is calculated to be 12. 

It is thus made evident that no valid calculation of relative atomic 
weights can be undertaken until molecular formulas can be determined. 
Lacking the essential criteria for such a determination, Dalton forges 
ahead with the bold assumption of an arbitrary set of maxims the 
"rule of greatest simplicity" with which the following passage is 
concerned. Today those postulates of Dalton that have already been 
examined are retained essentially intact; the rule of greatest simplicity 
is rejected. Yet it appears that one of Dalton's greatest single contribu- 
tions to the formulation of an atomic theory was made through this 
rule, and that his theory was most valuable in just that aspect in which 
it was most in error. Before examining the basis of this apparent para- 
dox, let us first consider the rule of greatest simplicity as it is outlined 
by Dalton in a continuation of the last excerpt. 

If there are two bodies, A and B, which are disposed to combine, the 
following is the order in which the combinations may take place, begin- 
ning with the most simple: namely, 

i atom of A + i atom of B = i [compound] atom of C, binary. 

1 atom of A + 2 atoms of B = i [compound] atom of D, ternary, 

2 atoms of A + i atom of B = i [compound] atom of E, ternary. 

i atom of A + 3 atoms of B = i [compound] atom of F, quaternary. 

3 atoms of A + i atom of B = i [compound] atom of G, quaternary. 

&c. &c. 

The following general rules may be adopted as guides in all our investi- 
gations respecting chemical synthesis. 


i st. When only one combination of two bodies can be obtained, it 
must be assumed to be a binary one, unless some cause appear to the 

2d. When two combinations are observed, they must be presumed to 
be a binary and a ternary. 

3d. When three combinations are obtained, we may expect one to be 
a binary, and the other two ternary. 

4th. When four combinations are observed, we should expect one 
binary, two ternary, and one quaternary, &c . . . 

yth, The above rules and observations equally apply, when two bodies, 
such as C and D, D and E, &c. are combined. 

Dalton now proceeds to show how, with these additional postulates, 
the calculation of atomic weights can be carried out. However, we 
possess a clearer, if more elementary, presentation of this material in 
the words of one of Dalton's contemporaries and admirers, Thomas 
Thomson. In 1807, a year before the appearance of Dalton's own book, 
Thomson published in the third edition of his System of Chemistry 
the first printed exposition of Dalton's ideas, and it was through this 
account that most of the scientific world first became familiar with 
Dalton's views. Throughout this account Thomson uses the terms 
"density of the atom" and "relative density of the atom" to signify 
"weight of the atom" and "relative weight of the atom" or "atomic 
weight," respectively. He says: 

We have no direct means of ascertaining the density of the atoms of 
bodies; but Mr. Dalton, to whose uncommon ingenuity and sagacity the 
philosophic world is no stranger, has lately contrived an hypothesis 
which, if it prove correct, will furnish us with a very simple method of 
ascertaining that density with great precision. Though the author has 
not yet thought fit to publish his hypothesis, yet as the notions of which 
it consists are original and extremely interesting, and as they are inti- 
mately connected with some of the most intricate parts of the doctrine 
of affinity, I have ventured, with Mr. Dalton's permission, to enrich this 
work with a short sketch of it. 

In justice to Mr. Dalton, I must warn the reader not to decide upon 
the notions of that philosopher from the sketch which I have given, de- 
rived from a few minutes' conversation, and from a short written 
memorandum. The mistakes, if any occur, are to be laid to my account, 
and not to his; as it is extremely probable that I may have misconceived 
his meaning in some points. [This gracious disclaimer was not entirely 
necessary; in so far as the present excerpt is concerned, Thomson seems 
to have given a surprisingly accurate account of the ideas entertained by 
Dalton in 1804.] 

The hypothesis upon which the whole of Mr. Dalton's notions respect- 
ing chemical elements is founded, is this. [It is interesting to observe 

232 CASE 4 

that Thomson here calls attention to the "rule of greatest simplicity" (a 
more detailed expression of the key idea of atom-to-atom combination) 
as the cornerstone of Dalton's theory. That is, to Thomson at least, there 
was nothing strikingly new or improbable about Dalton's other postu- 
lates, but the rule of greatest simplicity is recognized as an advance of 
pivotal importance.] When two elements unite to form a third substance, 
it is to be presumed that one atom of one joins to one atom of the other, 
unless when some reason can be assigned for supposing the contrary. 
Thus oxygen and hydrogen unite together and form water. We are to 
presume that an [a compound] atom of water is formed by the com- 
bination of one atom of oxygen with one atom of hydrogen. In like man- 
ner one [compound] atom of ammonia is formed by the combination 
of one atom of azote [nitrogen] with one atom of hydrogen. If we repre- 
sent an atom of oxygen, hydrogen, and azote, by the following symbols, 

Oxygen O 

Hydrogen O 

Azote (D 

Then an [a compound] atom of water and of ammonia will be repre- 
sented respectively by the following symbols: 

Water O0 

Ammonia GXD 

[These symbols represent a real departure. Although the alchemists 
had been accustomed to the use of symbols to represent indeterminate 
amounts of their "elements," Dalton's new symbols definitely refer to a 
single atom of the element symbolized; and instead of using new symbols 
for more complex substances, the composition of the compound is sys- 
tematically represented as a combination of the symbols for the atoms 
of which it is supposed to be composed. This representation also empha- 
sizes Dalton's concept of compound formation as the direct application 
or addition of an atom of one element to one or a few atoms of another 
element, rather than as a vague aggregate of indeterminate numbers of 
the particles of different elements.] But if this hypothesis be allowed, it 
furnishes us with a ready method of ascertaining the relative density of 
those atoms that enter into such combinations; for it has been proved by 
analysis, that water is composed of 85^ of oxygen and 14^ of hydro- 
gen. An [a compound] atom of water of course is composed of 85^ 
parts by weight of oxygen and 14^ parts of hydrogen. Now if it con- 
sist of one atom of oxygen united to one atom of hydrogen, it follows, 
that the weight of one atom of hydrogen is to that of one atom of oxygen 
as 14^ to 85%, or as i to 6 very nearly. In like manner an [a com- 
pound] atom of ammonia has been shown to consist of 80 parts of azote 
and 20 of hydrogen. Hence an atom of hydrogen is to an atom of azote 
as 20 to 80, or i to 4. Thus we have obtained the following relative 
densities of these three elementary bodies. 

Hydrogen i 

Azote .4 

Oxygen 6 


. . . Azote and oxygen unite in various proportions, forming nitrous 
oxide, nitrous gas, and nitric acid, 3 besides some other compounds which 
need not be enumerated. The preceding hypothesis will not apply to all 
these compounds; Mr. Dalton, therefore, extends it farther. Whenever 
more than one compound is formed by the combination of two elements, 
then the next simple combination must, he supposes, arise from the union 
of one atom of the one with two atoms of the other. If we suppose 
nitrous gas, for example, to be composed of one atom of azote, and one 
of oxygen, we shall have two new compounds, by uniting an [a com- 
pound] atom of nitrous gas to an atom of azote, and to an atom of 
oxygen, respectively. If we suppose farther, that nitrous oxide is composed 
oxide contains two atoms of azote united to one of oxygen, while 
nitric acid consists of nitrous gas and oxygen, united [compound] atom 
to atom, then the following will be the symbols and constituents of 
these three bodies: 

Nitrous gas CXD 

Nitrous oxide (DO0 

Nitric acid QDO 

The first gas consists only of two atoms, or is a binary compound, but 
the two others consist of three atoms, or are ternary compounds; nitrous 
oxide contains two atoms of azote united to one of oxygen, while 
nitric acid consists of two atoms of oxygen united to one of azote. [The 
compositions given for these compounds are entirely correct. This is one 
of the relatively few instances in which the rule of greatest simplicity 
yields a satisfactory formulation. However, in this case the interpretation 
of the rule could be guided by the approximately known values of the 
gaseous densities.] 

Thomson now proceeds to compare the analyses predicted by these 
formulas with those obtained empirically, and concludes that, within 
:he limits of the rather large experimental errors, a satisfactory agree- 
tnent obtains. 

Dalton s Contributions to the Atomic Theory. Dalton is usually 
denominated the "father of the atomic theory." Though the theory is 
venerable almost beyond measure, Dalton's deceptively simple but 
vital contributions to the atomic theory, as set forth in the passages, 
reproduced above, were indeed instrumental in the formulation of the 
lighly developed conceptual scheme we know today. Let us consider 
:he nature and value of Dalton's essential work. 

(i) Dalton contributed a notably plausible, precise, and unambigu- 
ous statement of the basic postulates of the atomic theory. The clarity 

8 "Nitrous oxide" signifies N 2 O. "Nitrous gas" signifies "nitric oxide," NO. "Nitric 
icid" signifies "nitrogen dioxide,'* NOa, the "red fumes" obtained when oxygen is added 
o "nitrous gas.*' This simple alphabetical symbolism for the elements and compounds 
vas suggested by Berzelius (whom we shall meet later in our story) as a convenient 
substitute for the much more cumbersome ideographic notation used by Dalton. 

234 CASE 4 

of the statement is, indeed, much more noteworthy than its content. 
We can see, by reference to the following famous passage from New- 
ton's Optic\s (1706), that in so far as content is concerned there is 
little in Dalton's preliminary statements (excluding the "rule of greatest 
simplicity") that is definitely new. Even the content of Newton's 
statement is little more than a paraphrase of a much older work 
Lucretius' De Rerum Natura (57 B.C.) which is in turn derived 
through Epicurus from Democritus and perhaps even more ancient 

That Dalton was familiar with, and impressed by, Newton's state- 
ment is demonstrated by the fact that the following excerpt from the 
Optic\s has been found in Dalton's notebook, transcribed by his own 

It seems probable to me that God in the beginning formed matter in 
solid, massy, hard, impenetrable, movable particles, of such sizes and 
figures, and with such other properties, and in such proportion to space 
as most conduced to the end for which he formed them; and that these 
primitive particles being solids, are incomparably harder than any porous 
bodies compounded of them; even so very hard as never to wear or 
break in pieces; no ordinary power being able to divide what God Him- 
self made One, in the first creation. While the particles continue entire 
they may compose bodies of one and the same nature and texture in all 
ages; but should they wear away or break in pieces, the nature of things 
depending on them would be changed. Water and earth, composed of 
old worn particles and fragments of particles, would not be of the same 
nature and texture now, with water and earth composed of entire par- 
ticles in the beginning. And therefore that nature may be lasting, the 
changes of corporeal things are to be placed only in the various separa- 
tions and new associations, and motions of these permanent particles; 
compound bodies being apt to break, not in the midst of solid particles, 
but where those particles are laid together, and only touch in a few 
points . . . 

God is able to create particles of matter of several sizes and figures, 
and in several proportions to the space they occupy, and perhaps of differ- 
ent densities and forces ... At least I see nothing of contradiction in 
all this. 

To be sure, as an inspirational declaration, Newton's statement is 
immeasurably superior to Dalton's. Moreover, some of the arguments 
advanced by Dalton in support of his hypothesis are seen to be almost 
certainly of derivative origin. But what of inspiration is lacking in 
Dalton's rather pedestrian prose is more than compensated by the 
lucidity and definiteness of his statements; by the fashion in which he 
strips his atoms of their aura of semidivinity, and reveals them as finite 
bodies many of whose attributes are knowable by man; and by his 


suggesting, through a clear statement of tentative axioms and rules of 
procedure, how such knowledge might be secured. 

(2) One crucial aspect in which Dalton's theory is a striking advance 
beyond all previous theories is in its major stress on one atomic prop- 
erty weight. Other theories (Newton's, for example) occasionally 
recognized weight as one of the properties of "ultimate particles," but 
it had never been singled out for special attention. Rather, it was con- 
sidered as one of many other properties, like size, shape ("figure"), 
color, hardness, wetness, motion, etc. As long as attention was diverted 
to any or all of this group of properties the theory was incapable of 
advancing with the then available empirical data. As it happened, a 
consideration of weight relations proved to be the fruitful line, and to 
the extent that Dalton made atomic weights the keystone of his theory, 
using them as the chief criterion for the distinction of one atomic species 
from another, he set his conceptual scheme on the road that led it to- 
ward the "validation" 4 denied all previous atomic theories. We may 
apprehend the narrowness of this privileged path when we observe 
that, to the extent that Dalton laid a subsidiary but by no means minor 
emphasis on the property of atomic size, he was led into a series of 
errors and contradictions that made it impossible for him to appreciate 
the significance of the subsequent investigations of Gay-Lussac and 

Probably we shall never completely understand how Dalton came to 
attach so much importance to weight, nor can we deny the possible 
intervention of chance. However, at least two factors that may have 
conditioned his response to the problems of his theory can be discerned. 
For one thing, recent experiments had shown that no appreciable 
weight was associated with the hypothetical "matter of heat" ("ca- 
loric"), so that the weight of an ordinary body or of its components 
acquired new significance, in so far as it was now more a character- 
istic constant, and no longer complexly variable with temperature. 
Even more important, in all probability, was the influence of Lavoisier's 
notable triumph over the phlogiston theory, largely achieved through 
the careful study of weight relations. But however Dalton may have 
been led to his new emphasis on atomic weights, there can be no ques- 
tion but that this stress was rapidly fruitful of a new usefulness for, 
and a new faith in, the atomic theory. 

(3) The rule of greatest simplicity is recognized by Thomson as the 

4 Words like "explain," "validate," "prove," "real," "correct," etc. will usually be 
enclosed in quotation marks, to suggest their association with the qualifying phrase: 
"what is meant in science when we say . . ." Some such qualification appears desirable 
because there are still unsettled philosophic issues that pertain to the precise significance 
of these words when they are used in connection with scientific conceptualization and its 
attendant processes. 

236 CASE 4 

heart of Dalton's new theory, and it was indeed an invaluable contri- 
bution to the development of the atomic theory. As already observed, 
this rule, of all Dalton's basic postulates, is the most arbitrary and the 
least "correct." Yet, for the time at which it was stated, the rule repre- 
sented a bold and intelligent choice of a simplifying assumption. 

The rule is in no way an essential part of an atomic theory as such, 
but it exercised the vital function of providing the molecular formulas, 
however mistaken, which were absolutely essential for the operations 
of an atomic theory that lacked any more rational method for the 
evaluation of such formulas. Using the formulas provided by his rule 
Dalton was able to bring the simple abstract concept of atoms to bear 
upon the difficult concrete problem of determining atomic weights. We 
shall soon see that it was also this rule which led the atomic theory to 
its decisive test and greatest triumph the prediction of the law of 
multiple proportions. 

The use of an arbitrary simplifying assumption like the rule of 
greatest simplicity is a tactical device not infrequently applied in the 
earlier stages of a difficult scientific enterprise. When the complexity 
of the data confronting the investigator appears to exceed the bounds 
of human comprehension, one of the few courses open to him is to 
consider the situation in a grossly oversimplified way, using arbitrary 
working rules as a mechanism for the organization, assessment, and 
comprehension of his data. The creation of such rules may come as an 
emotional response to a naive faith in the simplicity of nature, or as a 
conscious attempt to sift certain regular relations from a disorganized 
mass of data. With Dalton, the framing of the simplifying assumption 
was almost certainly due to a belief in the "regularity and simplicity 
generally observable in the laws of nature" (New System], and some 
of the most sophisticated conceptual advances of recent years have first 
appeared in an oversimplified form. 

To the extent that Dalton's arbitrary "rule" was the simplest assump- 
tion permitting further progress, it was the best possible assumption. 
It was not in itself implausible; and, in commenting on an analogous 
situation in modern science, T. W. Richards, the first American Nobel 
Prize winner in chemistry, has very justly remarked: 

"Whether or not it [a provisional hypothesis] may be a nearer ap- 
proach to a definite picture of reality is a question of less importance 
than that concerning its ability to suggest new experimental work, 
and thus to lead to new generalization based upon fact. Hypotheses 
are temporary in their very nature; it has been said that science is being 
built up of stones taken from their ruins. Perhaps it might rather be 
said that hypotheses are the scaffolding which the scientific man erects 
around the growing solid structure, enabling him to build more swiftly 


and freely. Danger can arise from the use of such temporary assistance 
only when the builder confounds the temporary with the permanent, 
and builds one into the other in such a way that the collapse of one 
injures the other; or when the scaffolding is so badly constructed as 
not to bear a reasonable weight for a reasonable time." 

When the theory becomes capable of supporting itself the provisional 
working rules and hypotheses may be incorporated, amended, or dis- 
carded entirely in the light of the fuller understanding which they 
have made possible. The inadequacy of Dalton's "rule" ultimately 
became apparent, but only after it had served the purpose for which 
it was created. 

(4) One last contribution of Dalton's, the importance of which 
should not be underestimated, was his development of a simple sym- 
bolism for the representation of atoms and their combinations. Dalton's 
symbols have since been replaced by more serviceable ones; but, in 
the early days of his atomic theory, his symbols made it possible for 
scientists to manipulate atoms, on paper, in a simple, economical and 
meaningful fashion. As already remarked (page 232), these symbols 
also serve to represent compounds as direct atom-to-atom combinations. 

Students of semantics have called attention to the dangers arising 
from the mistaken feeling that, in handling symbols, we are in effect 
dealing with the realities they are intended to represent. The danger 
is undeniable; but it also seems plain that by providing atomic symbols 
and rules for their manipulation, Dalton encouraged his contemporaries 
to acquire a faith in the reality, significance, and usefulness of atoms. 


The Impact of the Atomic Theory. So far we have considered 
the origin of what is generally called Dalton's atomic theory, the con- 
tent of that theory, the means by which it was applied to the determina- 
tion of atomic weights, and the extent of Dalton's own contributions 
to the theory. We may now examine the services that the new atomic 
theory was able to perform in the scientific world in which it appeared, 
and the way in which it was received by that world. 

Considering the long delays and hard struggles that occurred before 
the general adoption of Lavoisier's antiphlogistic hypothesis, the com- 
parative rapidity with which the atomic theory won more or less 
general assent is somewhat surprising. However, there are several major 
differences in the two stories. Lavoisier sought to displace a strongly 
entrenched and generally accepted theory; Dalton's theory replaced 
nothing but, rather, grew by leaps and bounds in a scientific environ- 
ment that had long nourished an implicit qualitative atomism. Further- 

238 CASE 4 

more, while the phlogiston theory could "explain" the facts almost as 
well as the antiphlogiston theory, albeit in a somewhat more complicated 
fashion, Dalton's hypothesis accounted for two broad empirical gen- 
eralizations that were already in unexplained existence, and suggested 
yet a third. In this respect the atomic theory was indeed the creation 
of the "skilful observer" mentioned in Dalton's curiously modern ap- 
praisal of the dynamic nature of a scientific advance: 

Facts and experiments, however, relating to any subject, are never duly 
appreciated till, in the hand of some skilful observer, they are made the 
foundation of a theory by which we are able to predict the results and 
foresee the consequences of certain other operations which were never 
before undertaken. 

One other striking difference between the situations of Lavoisier and 
of Dalton lies in the former's great ability as an experimentalist a 
skill that allowed him to buttress his theory with his own brilliant 
experiments. Dalton, on the other hand, did not begin the serious 
study of chemistry until 1795, and never became a very able laboratory 
worker. Fortunately, Dalton's shortcomings in this respect were not 
of major importance because, as explained by his biographer, William 

his experiments, though wanting the exactitude of modern research, were 
not unskilfully devised and were most sagaciously interpreted. 

They were, perhaps, such as were most needed at the close of the last 
century, when so many fields of experimental research were untilled, that 
bold tentative incursions into new domains of thought, large groupings, 
and happy generalizations of approximate results were more effective 
instruments of advance than scrupulous precision in details. 

Thus Dalton secured his position not so much through his own experi- 
ments but, rather, by showing prospective doubters how their own 
experimental results could be most readily interpreted with the aid of 
certain "large groupings and happy generalizations." Although, owing 
to the inaccuracy of the analyses and f aultiness of the assumptions on 
which they were based, Dalton's atomic weights were well wide of the 
mark, his theory possessed a fundamental soundness that made it 
extraordinarily useful and attractive as the first rationalization of three 
of the major generalizations of experience that form the basis of 
modern chemistry. To these let us now turn. 

The Law of Definite Proportions. It has long been an implicit 
article of faith among chemists that a given compound always con- 
tained its components in fixed proportion by weight for example, 
that the weights of hydrogen and oxygen prtsent in i gram of water 
would not vary with the source of the water. This assumption underlies 


the careful analytic work of Lavoisier and his contemporaries, but its 
general applicability had never been established. At the turn of the 
nineteenth century this implicit assumption became the subject of a 
famous dispute between two French chemists Berthollet and Proust. 
Berthollet based his arguments on his theory of "chemical affinity" and 
on the obvious experimental fact that a metal heated in air undergoes 
oxidation gradually, yielding products in which the oxygen-to-metal 
ratio appears to be continuously variable up to a fixed maximum value. 
He contended that there was an infinite series of, for example, copper 
oxides with progressively variable colors and progressively variable 
weight proportions. This point of view was disputed by Proust, who 
demonstrated experimentally that all of these apparently distinct cop- 
per oxides actually contained just two oxides of copper, each of invariant 
composition. Proust maintained that the "compounds" of continuously 
variable oxygen-to-copper ratio reported by Berthollet were actually 
nothing but variable mixtures of just two compounds in which the 
oxygen-to-copper ratio had two discrete but invariant values. He also 
asserted that the other cases of this class to which Berthollet had called 
attention could be similarly explained, and he buttressed his position 
by demonstrating the identity of composition of certain materials of 
synthetic (laboratory) origin and the same materials derived from 
natural (mineral) sources. Proust defines his position in the following 
trenchant declaration. 

According to our principles a compound ... is a privileged product 
to which nature assigns fixed ratios; it is, in short, a being which Nature 
never creates even when through the agency of man, otherwise than 
with her balance in hand, pondere et mesura. Let us recognize, there- 
fore, that the properties of true compounds are invariable as is the ratio 
of their constituents. Between pole and pole, they are found identical in 
these two respects; their appearance may vary owing to the manner of 
aggregation, but their [chemical] properties never. No differences have 
yet been observed between the oxides of iron from the South and those 
from the North. The cinnabar of Japan is constituted according to the 
same ratio as that of Spain. Silver is not differently oxidized or muriated 
in the muriate of Peru than in that of Siberia. . . . 

We shall . . . concur in the belief that if the combinations which we 
make every day in our laboratories have a perfect resemblance to those 
of nature, this is due to the fact that the powers of nature hold invisible 
sway over all the operations of our arts. If we find it impossible to make 
an ounce of nitric acid, an oxide, a sulfide, a drop of water, in ratios 
other than those which nature had assigned to them from all eternity, 
we must again recognize that there is a balance which, subject to the 
decrees of nature, regulates even in our laboratories the ratios of corn- 
founds. And even if some day we should succeed in clearly recognizing 

240 CASE 4 

the causes which retard or accelerate the action of substances tending to 
combine, we could only flatter ourselves with knowing one more thing, 
namely, the means which nature uses to restrict compounds to the ratios 
in which we find them combined. But such knowledge, would it invali- 
date the principle I have proved? I think not, because the principle is 
only the corollary of the facts which we discover every day; there is 
nothing hypothetical about It; facts have led to it, facts alone could 
overthrow it. 

To another group of materials cited by Berthollet the alloys, amal- 
gams, and glasses Proust quite correctly denied the status of "com- 
pound." These substances showed no evidence of bearing their 
components in fixed proportions, nor did they appear to be mixtures 
of compounds of fixed compositions. Such materials are now known 
to be solutions of one solid in another, and just as the amount of salt 
dissolved in water can be varied continuously up to a limit fixed by 
the solubility of salt in water, the composition of an alloy, amalgam, 
or glass can be similarly varied. Proust very wisely refrained from say- 
ing why there resulted in some cases chemical compounds of fixed 
composition, inseparable except by chemical means, and in others 
physical mixtures of variable composition and separable by physical 
means. However, while adroitly side-stepping this speculative issue, 
he stressed the importance of the distinction between mixtures and 

But what difference, it will be asked, do you recognize between your 
chemical combinations [compounds] and the unions of combinations 
[mixtures of compounds] which latter you tell us nature restricts to no 
fixed ratios? 

Is the power which makes a metal dissolve in [react with] sulfur 
different from that which makes one metallic sulfide dissolve in an- 
other? I shall be in no hurry to answer this question, legitimate though 
it be, for fear of losing myself in a region not yet sufficiently lighted up 
by the facts of science; but my distinctions will, I hope, be appreciated 
when I say: The attraction which causes sugar to dissolve in water may 
or may not be the same as that which makes a fixed quantity of carbon 
and of hydrogen dissolve in [react with] another quantity of oxygen to 
form the sugar of our plants, but what we do see clearly is that these 
two kinds of attractions are so different in their results that it is im- 
possible to confound them. 

What bearing does this controversy, leading to the conclusion that 
there are chemical "compounds" with definite, invariant weight pro- 
portions, have on the atomic theory? 

(i) A clear definition of a chemical compound, as distinct from a 
mixture, was created. The application of the atomic theory to com- 


pounds was fruitful; its immediate application to mixtures would prob- 
ably have been futile and confusing. 

(2) As a result of the enormous labors of Proust and others, under- 
taken to maintain their respective positions in the controversy, there was 
secured a vast body of analytical information which later served as grist 
for the mill of the atomic theory. 

(3) The controversy called the attention of the learned world to the 
existence of a large number of cases in which two elements were capable 
of combining in more than one proportion. Some instances of the for- 
mation of multiple compounds had been known previously; but now 
such multiplicity of compounds of the same elements was shown to be 
a quite general phenomenon, and one that fairly clamored for an ex- 
planation. Such an "explanation" was, as we shall see, furnished by the 
atomic theory. 

(4) Last, and probably most important, is the consideration that 
Dalton's theory had the advantage that the law of definite or invariant 
proportions was a logical deduction from his postulates: the weight 
of the atoms of a given element is invariant; and the rule of greatest 
simplicity suggests that compounds are formed by the combination of 
fixed numbers of different atoms. By the time (1807) when Dalton's 
theory reached the scientific world, opinion on the Berthollet-Proust 
controversy had begun to run quite definitely in the latter's favor 
and it was thus an item of credit to the atomic theory that it was in 
harmony with Proust's findings. It would, of course, be incorrect to 
say that the law of definite proportions "proved" the correctness of the 
atomic theory, since, as we have seen, the theory contained the law 
among its axioms. But, contrariwise, it is difficult to see how any theory 
that denied the existence of atoms could have accommodated the law 
of definite proportions in a more elegant and convincing manner. 

The Law of Equivalent Proportions. Another major generalization 
of analytic experience, which also antedated the development of Dal- 
ton's atomic theory, was progressively disclosed by Richter in a series of 
papers published between 1792 and 1802. This generalization repre- 
sented the culmination of a prolonged and widespread study of a special 
class of chemical reactions (acid-base neutralizations). In the latter half 
of the eighteenth century the quantitative data on these reactions, col- 
lected by Cavendish and others, prompted several workers to give 
various partial statements of the law of equivalent proportions. How- 
ever, it remained for Richter, an obscure German chemist, to recognize 
the full generality and importance of the mathematical relations be- 
tween the quantities of various substances that reacted with one an- 

The type of experimental data that formed the basis for Richter's 

242 CASE 4 

generalization is best suggested by a hypothetical instance. Suppose that 
experiments are performed with two substances, A and B, each of 
which is capable of reacting chemically with either of two other sub- 
stances, C and D. There are then four reactions to be studied: A with 
C) B with C; A with D, and B with D. In each case a measurement is 
made of the weight of one of the materials which reacts completely 
with a given weight of the other substance. By "reacts completely" we 
mean that both of the starting materials are completely expended, so 
that no residue of either is present at the conclusion of the experiment. 
From four such determinations, the following results might be 

50 grams of A react completely with 33 grams of C, 

75 grams of B react completely with 33 grams of C, 

64 grams of A react completely with 26 grams of D, 

96 grams of B react completely with 26 grams of D. 

It is apparent that there is a striking relationship among these figures, 

75 9 6 " 

From the unorganized mass of empirical data available to him, Richter 
successfully separated a number of such coordinated sets of values. In 
most instances the ratios were not as simple as the 2:3 ratio involved in 
the illustrative example; but, in general, the internal consistency of the 
experimental data was most impressive. The existence of these regulari- 
ties suggested, and served to justify, a statement of a law of equivalent 
proportions, which may be paraphrased as follows : //, for any two sub- 
stances, there are certain weights that are equivalent in their capacity 
for reaction with some third substance^ the ratio of such weights is the 
same regardless of what the third substance may be. 

Whether Dalton was aware of Richter's work at the time when the 
atomic theory was being developed is uncertain. Until 1802 Richter's 
results were apparently either almost completely unknown or ignored 
even in Germany, where they had been published; and the balance of 
the available evidence indicates that Dalton first learned of Richter's 
work after the atomic theory was essentially completed. When con- 
sidered in the light of this theory, however, it was apparent that Rich- 
ter's generalization, like that of Proust, was in essential harmony with 
the concepts of the atomic theory. 

Thus, on Dalton's atomic theory, it is only necessary to hypothesize 
that, when quantities of two substances display equivalent capacities 
for reaction, there are present equal numbers of molecules of the two 


species. It is easy to see how this works out in the illustrative example 
cited above. It is plain that the equivalent quantities of A and B, de- 
fined by the reaction of these substances with equal weights of C, stand 
in the ratio 50 : 75, on : i l / 2 . If these quantities oiA and B contain equal 
numbers of their respective molecules, then each molecule of B must 
be i l / 2 times as heavy as one molecule of A. This suggests that any 
time we have equivalent quantities of A and B i.e., equal numbers 
of the two kinds of molecule the weight of A will stand to that of 
B as i : i l / 2 . But this constancy of the ratio of the weights of equivalent 
amounts of the two substances is the very import of the law of equiva- 
lent proportions. Once again, therefore, the atomic theory is found to 
accord well with experience. 

The Law of Multiple Proportions. Unlike the two laws considered 
above, the law of multiple proportions was not fully apprehended until 
after Dalton's atomic theory had indicated its probable existence. The 
experimental confirmation of this prediction resulted in an immeasur- 
able strengthening of the position of the atomic theory. 

The prediction of this law is a logical outgrowth of the rule of 
greatest simplicity, in which Dalton recognizes the possibility that the 
atoms of two elements may combine in more than one numerical pro- 
portion, giving rise to two or more compounds of the same two ele- 
ments. As we have already seen, the fairly frequent occurrence of such 
families of compounds was revealed by the work of Proust and others. 
However, while Proust had observed that two elements might combine 
in more than one weight proportion, Dalton now showed that the 
different fixed proportions were not independent entities, but, rather, 
that they were related to each other in a simple way that was readily 
understood in terms of the atomic theory. 

A modern statement of the law of multiple proportions might run: 
"When two elements unite to form more than one compound, the 
weights of one element that combine with a fixed weight of the other 
element in the different compounds are in the ratio of small whole 
numbers." Now, Dalton had hypothesized that compounds were 
formed by the combination of definite small numbers of atoms of 
characteristic fixed weights. Thus, let us imagine that the elements A 
and B form two compounds, AB and A%B. In compound AB one atom 
of A is united with each atom of J5, but in compound A%B two atoms 
of A are combined with one of B. If, now, we consider the number of 
atoms of A that react with a fixed number of atoms of B (i.e., with 
some fixed weight of 5), it is plain that in the formation of compound 
A 2 B there will be required twice as many atoms of A as are needed to 
form compound AB. Consequently, in combining with a fixed weight 
of element B, the weight of A expended in forming compound A%B 

244 CASE 4 

will stand to that required in the formation o compound AB in the 
very simple ratio 2:1. Consideration of other such cases indicates that 
the law of multiple proportions is a necessary consequence of the basic 
postulates of Dalton's atomic theory. Somewhat more complicated 
ratios, like 2 : 3 or 3 : 4, are also to be expected on occasion; but the rule 
of greatest simplicity definitely suggests that the ratios will always be 
simple ones, involving only small numbers. Had the predicted ratios 
been something like 24 : 25 or 87 : 88 it would have been quite hopeless 
to search for them in the relatively crude analyses of Dalton and his 
contemporaries. However, in its prediction of simple, readily perceived 
ratios, the rule of greatest simplicity more than justified its existence by 
stimulating the quest for such ratios. This quest rapidly proved to be 
very fruitful. 

Curiously enough, when, some fifteeen years earlier, the existence 
of a law of multiple proportions was intimated by William Higgins, 
his suggestion attracted no attention whatever. Part of this neglect can 
be attributed to the fact that Higgins's reference was purely incidental 
to a discussion of Lavoisier's oxygen theory, which was then the cyno- 
sure of all scientific eyes. Furthermore, it appears that Higgins con- 
tented himself with the bare assertion of this relation, and made no 
attempt to provide it with an experimental "validation." An interesting 
appraisal of the contributions of Higgins and of Dalton is available 
in a paper by W. H. Wollaston that appeared in the Philosophical 
Transactions of the Royal Society, in 1814 some years after the 
events referred to. 

The first instance in which the same body was supposed to unite with 
different doses of another, in such proportions that one of these doses 
is a simple multiple of the other, was noticed by Mr. Higgins, who con- 
ceived, rather than actually observed to occur, certain successive degrees 
of oxidation of azote, and represented the series of its combinations with 
oxygen to be 

Azote i with 2 oxygen making nitrous gas. 

Azote i with 3 oxygen making red nitrous vapour. 

Azote i with 4 oxygen making yellow nitrous acid. 

Azote i with 5 oxygen making white nitric acid. 

He at the same time added his opinion, that such are the proportions 

in which these gases unite to each other by bul\ [i.e., by volume], having 

before observed one instance of union by exactly double bulk in the 

formation of water by the combustion of hydrogen and oxygen, and 

expressed his persuasion that the number of particles in a given bulk 

of the different gases is the same, and that the number of particles in 

the compounds of azote and oxygen, are successively in the proportions 

above stated. 

But though Mr. Higgins, in the instance of the union of hydrogen 


with oxygen, anticipated the law of bulks observed by M. Gay-Lussac 
[see Section 3], with respect to the union of gases, and in his conception 
of union by ultimate particles clearly preceded Mr. Dalton in his atomic 
views of chemical combination, he appears not to have taken much 
pains to ascertain the actual prevalence of that law of multiple propor- 
tions by which the atomic theory is best supported, and it is in fact to 
Mr. Dalton that we are indebted for the first correct observation of such 
an instance of a simple multiple in the union of nitrous gas with oxygen, 
In his endeavours to determine the composition of the atmosphere, he 
found that the quantity of oxygen contained in 100 measures of com- 
mon air would combine with either 36 or 72 measures of nitrous gas, 
according to certain variations in the mode of conducting the experi- 

Dalton's studies of the reaction of nitrous gas with oxygen were 
carried out in the years 1801-1804, during the very time when his 
atomic theory was being formulated. Shortly afterward Dalton dis- 
covered another pertinent case of such simple proportions. In his study 
of two gases, methane and ethylene, he found that the weight of hydro- 
gen that combined with a fixed weight of carbon to form methane was 
just twice as great as the weight of hydrogen that combined with the 
same weight of carbon in ethylene. It was the great strength of Dalton's 
position, however, that his demonstration of the application of his 
theory was not limited to the results of his own rather imperfect ex- 
periments. He was soon able to show that the working of the law of 
multiple proportions might be detected in analyses previously reported 
by other investigators. Such an instance was presented by the carbon 
oxides. The analysis of carbon dioxide ("carbonic acid," "fixed air") 
by Lavoisier had yielded results of 28 percent by weight of carbon and 
72 percent of oxygen. Carbon monoxide ("carbonic oxide"), the heavy 
inflammable "air" with which Priestley confounded Lavoisier, had 
been identified and analyzed in 1801 by Clement and Desormes, who 
reported its composition as 44 percent of carbon and 56 percent of 
oxygen. Dalton remarks, in his notes for the nineteenth of his lectures 
at the Royal Institution: 

Experience confirmed the truth of Lavoisier's conclusion that 28 parts 
charcoal + 72 oxygen constituted carbonic acid; also that carbonic oxide 
contained just half the oxygen that carbonic acid does, which indeed had 
been determined by Clement and Desormes, two French chemists, who 
had not, however, taken notice of this remarkable result. 

From the percentages cited before the last quotation, the foundation 
of Dalton's confident statement is far from evident, and it is not sur- 
prising that the "remarkable result" had long lurked unsuspected in 
the raw data. Yet the essential relation of the two weights of oxygen 

246 CASE 4 

is at once apparent when the analyses are reduced to the common basis 
of a fixed weight of carbon. This simple recalculation is Dalton's sug- 
gestion, and is performed, as follows. In carbon dioxide, 72 grams of 
oxygen are combined with 28 grams of carbon, or 2.57 grams of oxygen 
with i gram of carbon. In carbon monoxide, 56 grams of oxygen unite 
with 44 grams of carbon, or 1.27 grams of oxygen with i gram of carbon. 
The weights of oxygen reacting with i gram of carbon 2.57 and 
1.27 grams, respectively are then seen to stand in the ratio 2.02 : i, or 
very nearly 2:1. 

Owing to the inaccuracies of the analyses on which the calculations 
are grounded, the relation here, and elsewhere, is not exactly the simple 
ratio predicted; but as an increasing number of such sets of data were 
examined, it was apparent that the results showed an overwhelming 
tendency toward simple ratios. There is a moral in all this. Though 
facts may help to pave the road for a conceptual advance, the accumu- 
lation of facts does not, in and of itself, constitute or guarantee a con- 
ceptual advance. We must allow Santayana's rather cynical appraisal: 
"The empiricist . . . thinks he believes only what he sees, but he is 
much better at believing than at seeing." Not knowing what there was 
to see, diverted by a mode of (percentage) calculation that hid the 
inner harmony of their data, distracted by results that only approxi- 
mated the correct values, Proust and his contemporaries held the 
critical data in their hands and failed to see the significance of what 
they "knew." With the advent of Dalton's atomic theory, the new 
beliefs it encouraged brought about a remarkable sharpening of the 
empiricists' vision. They were told what to look for, and where and 
how to look for it and, behold, it was there. Dalton's obvious con- 
tribution, a new method of calculating analytical results, seems almost 
contemptible; but his more fundamental contribution was the powerful 
stimulus to investigation provided by his conceptual scheme. 

Before long there appeared new and better analyses, which helped to 
solidify the position of the law of multiple proportions. A particularly 
important series of determinations showed that the law of multiple 
proportions applied not only to the combinations of gases, but also, to 
the major class of acid-base reactions. Many of these reactions result 
in the formation of two kinds of salts, distinguished as "acid" and 
"normal." The general case is easily understood from an examination 
of one specific instance. Thus, sodium carbonate (Na 2 CO 3 , washing 
soda) is a normal salt; sodium bicarbonate (NaHCO 3 , baking soda) 
is an acid salt. If we consider the weights of sodium (Na) combined 
with a fixed weight of carbonate (CO 3 ) in these compounds, it is 
evident that the sodium-to-carbonate ratio is twice as great in sodium 
carbonate as in sodium bicarbonate. This, then, is another instance of 


simple multiple proportions, and its extension to the general case pre- 
sents no difficulty. Thus, letting M represent some metal, and A some 
acid group, while H as usual represents hydrogen, then if salts such as 
M 2 A and MHA are formed, the weights of M combined with the same 
weight of A in the two compounds are as 2 to i respectively; and, 
conversely, the weights of A combined with a fixed weight of M are 
as i to 2. 

A first report on pairs of salts of this character was made early in 
1808 by Thomas Thomson; two weeks later W. H. Wollaston reported 
a very considerable series of similar experiments which yielded results 
in excellent agreement with the law of multiple proportions. The be- 
ginning of Wollaston's communication to the Royal Society is of par- 
ticular interest, and is here reproduced. 

In the paper which has just been read to the Society Dr. Thomson, 
has remarked, that oxalic acid unites to strontian as well as to potash in 
two different proportions, and that the quantity of acid combined with 
each of these bases in their super-oxalates, is just double of that which 
is saturated by the same quantity of base in their neutral compounds. 

As I had observed the same law to prevail in various other instances 
of super-acid and sub-acid salts [acid and normal salts respectively], I 
thought it not unlikely that this law might obtain generally in such 
compounds, and it was my design to have pursued the subject with the 
hope of discovering the cause to which so regular a relation might be 

But since the publication of Mr. Dalton's theory of chemical combina- 
tion, as explained and illustrated by Dr. Thomson (Thomson's Chem- 
istry . . .) the inquiry which I had designed appears to be superfluous, 
as all the facts that I had observed are but particular instances of the 
more general observation of Mr. Dalton, that in all cases the simple 
elements of bodies are disposed to unite atom to atom singly, or, if either 
is in excess, it exceeds by a ratio to be expressed by some simple multiple 
of the number of its atoms. 

It appears from this passage that Wollaston was an independent 
discoverer of at least part of the law of multiple proportions. His state- 
ment is also of particular interest because it suggests the way in which 
a successful theory makes it possible to (in Dalton's words, quoted on 
page 32) "predict the results and foresee the consequences of certain 
other operations which were never before undertaken ." Thus Wol- 
laston, having found his preliminary experiments in complete accord 
with Dalton's theory, abandons his projected investigation as an act 
of supererogation. In this respect a successful conceptual scheme both 
encourages and discourages experimental work: on the one hand, it 
stimulates and directs the experiments by which it may be tested; 

248 CASE 4 

but once having sustained these tests, it stands in lieu of a host of 
further experiments that can be omitted in favor of others more apt to 
be productive of unpredictable facts and new ideas. 

In one last episode in the early history of the modern atomic theory 
we may observe the profound initial impact of the theory on a keen 
mind previously unaware of it. This is the mind of the Swede Berzelius, 
the titan among theoretical and experimental chemists of the early 
nineteenth century. Berzelius, writing in 1811, says: 

Berthollet, who is one of the most celebrated chemists of our age, in 
the course of his ingenious investigations into the laws of affinity, has 
attempted to demonstrate that substances could combine in an infinite 
number of continuous ratios. But Proust, another authority in chemical 
science, has proved on the contrary, that no such infinite variations occur 
in Nature, but that all complex definite substances [compounds] con- 
tain their fundamental constituents in a fixed ratio. . . . The truth of 
Proust's view cannot have failed to strike the experienced chemist; but 
what so far had not been known was, whether these sudden changes in 
composition occurred according to one and the same law for all sub- 
stances, or in some indeterminate manner peculiar to each substance. . . . 

I have been attracted to these investigations . . . through finding that 
in the basic chloride of lead and in the basic chloride of copper the acid 
is saturated by four times as much of the base as in the neutral salts. 
[The neutral and basic salts with which Berzelius worked bear to each 
other a relationship which is entirely analogous to that of the normal 
and acid salts already discussed. Berzelius here reports another inde- 
pendent discovery of a case of multiple proportions. However, it appears 
that neither he nor Wollaston realized the general prevalence of such 
relationships prior to their respective introductions to Dalton's atomic 

I had hoped to discover the cause of so remarkable a relation by accu- 
rately investigating the result of mixing different substances of this sort. 
Whilst engaged in this work I came across Nicholson's Journal for 1808 
and found in it the experiments of Wollaston on acid salts which had 
been suggested by Dalton's hypothesis. [This is not quite correct; Wol- 
laston apparendy began his v/ork before hearing of Dalton's atomic 
theory.] This hypothesis affirms that if substances can be made to com- 
bine in different ratios, these ratios are always produced by simple 
multiplication of the weight of the one substance by I, 2, 3, 4, etc. 
[Berzelius here gives an oversimplified account of the law of multiple 
proportions, which did not exclude somewhat more complicated ratios, 
like 2:3, 3:4, etc.] Wollaston's experiments seem to support this hypothe- 
sis. But such a doctrine of the composition of compounds would so 
illuminate the province of affinity, that supposing Dalton's hypothesis 
be found correct, we should have to look upon it as the greatest advance 
that chemistry has ever yet made in its development into a science. I 


have no knowledge whatever of how Dalton developed his theory and 
on what experiments he has based it, and hence I cannot judge whether 
my own experiments confirm his hypothesis in its full extent, or whether 
they modify it in a greater or less degree. 

Berzelius took effective steps to put an end to his ignorance, obtain- 
ing a copy of the New System directly from its author. In 1812, a year 
later, we find him writing to Dalton: 'The theory of multiple propor- 
tions is a mystery but for the Atomic Hypothesis, and as far as I have 
been able to judge, all the results so far obtained have contributed to 
justify this hypothesis." 

Berzelius' growing knowledge of Dalton's atomic theory is of interest 
because of the light it throws on the state of scientific communications 
in the epoch of the birth of the atomic theory. Berzelius, in Sweden, 
learns of Wollaston's work only some two or three years after the 
publication of the latter's results. This delay is not inconsiderable, 
though it should be remembered that this was the period of the Napo- 
leonic Wars. It appears, however, that the liaison between scientific 
workers on the two sides of the Channel was maintained with some 
success. Thus in 1809 we find Thomson writing to Dalton: "I write 
you at present to give you some information respecting your atomic 
theory . . . Berthollet has written a long attack upon it in the intro- 
duction to the French translation of my "System of Chemistry," a 
book which I have not yet seen and cannot therefore give you any 
account of his arguments ..." That is, the first published account of 
Dalton's atomic theory, appearing in England in 1807, has been brought 
to the attention of Continental chemists in a translation completed by 
1809. It appears that this translation did not reach Berzelius in Sweden, 
but he was able to secure further information about the atomic theory 
directly from Dalton. 

In general, Dalton's "explanation" of the laws of definite, equivalent, 
and multiple proportions was welcomed by a generation of chemists 
hard pressed by too great an abundance of "facts" and with all too few 
generalizations in terms of which the "facts" might be construed. To 
be sure, there were protests such as that of Berthollet, who saw in 
Dalton's work the vindication of Proust's position. Such protests were 
soon heard no more; but there were other, more persistent voices that 
objected with good reason, and could not be stilled. Thus Davy, Gay- 
Lussac, Wollaston, and others, though impressed by the achievements 
of the atomic theory, objected to its general conjectural character, and 
particularly expressed their doubts about that part of Dalton's atomic 
theory which, in its youth, had been one of its great sources of strength, 
but which, in its maturity, was seen to be its greatest weakness the 

250 CASE 4 

"rule o greatest simplicity." While the experimental data from which 
the atomic weights were computed might be refined, the meaningful- 
ness of these weights would remain doubtful as long as the interpretation 
of the analytic data rested upon molecular formulas furnished by an 
arbitrary, highly speculative, working rule. Dalton, in the second part 
of his New System, published in 1810, recognizes this shortcoming. 
After remarking that 

As only one compound of oxygen and hydrogen is certainly known, it 
is agreeable to the ist rule [see page 25] that water should be concluded 
a binary compound; or, one atom of oxygen unites with one of hydrogen 
to form one of water. Hence the relative weights of the atoms of oxygen 
and hydrogen are 7 to i ... [observe that Dalton is using as the com- 
bining weights i of hydrogen to 7 of oxygen, rather than the cruder 
proportion of i to 6 that he had employed earlier], 

he goes on to say: 

After all, it must be allowed to be possible that water may be a ternary 
compound. In this case, if two atoms of hydrogen unite to one of oxygen, 
then an atom of oxygen must weigh 14 times as much as one of hydro- 
gen; if two atoms of oxygen unite to one of hydrogen, then an atom of 
oxygen must weigh 3^/2 times one of hydrogen. 

Further extension of the usefulness of the atomic theory was in- 
separably connected with the possibility of placing its molecular formu- 
las and atomic weights on a more strictly rational foundation. Dalton 
himself was unable to suggest such a basis. The discovery, by another 
investigator, of the cornerstone of a more permanent foundation is the 
subject of the next section. The scene shifts to France, where the great 
pneumatic chemist Gay-Lussac holds the center of the stage. 


In 1808 Gay-Lussac announced his discovery of a simple regu- 
larity in the combining proportions of gases. It was this observation 
that, when correctly interpreted, led to a sounder criterion for the 
establishment of molecular formulas (and, thence, of atomic weights) 
than was provided by Dalton's "rule of greatest simplicity." 

Gay-Lussac asserts that he was led to a general study of combining 
volumes in gas reactions by the result of an investigation of the combin- 
ing proportions of hydrogen and oxygen which he and Alexander von 
Humboldt had completed three years before. This earlier work was 
carried out in order to ascertain the accuracy of a promising method 


for determining the oxygen content of "airs." Cavendish and others 
(including Dalton) had shown that the analyses derived from Priest- 
ley's "nitrous air test" were subject to large uncertainties, since the re- 
sults were strongly influenced by small changes in the experimental 
conditions. Volta had proposed an alternative approach, based on a 
measurement of the volume contraction produced when a measured 
quantity of the gas under analysis was exploded with excess hydrogen. 
Such determinations could be conducted conveniently and accurately 
with the Volta eudiometer a graduated tube like Priestley's nitrous 
air eudiometer, but with the addition of sparking terminals sealed 
through the glass* 

The excellence of this method and technique was amply demon- 
strated by Gay-Lussac and von Humboldt in a research conducted with 
exemplary skill and thoroughness. Taking care to maintain constant 
temperature and pressure throughout each experiment, they found 
that the more carefully their experiments were performed, the closer 
was the approach to the very simple combining proportion of just two 
volumes of hydrogen per volume of oxygen their best figure being 
1.9989 volumes of hydrogen per i.oooo volume of oxygen. With this 
datum, and with the knowledge that several other gas reactions in- 
volved volume proportions that roughly approximated simple ratios, 
Gay-Lussac apparently came to hope that with more exact measure- 
ments it would be found that volumetric combining proportions of 
great simplicity prevailed in the generality of gas reactions. 

His hope was founded on sound theoretical arguments. It was be- 
lieved, quite correctly, that there were forces of attraction, or cohesion 
between the ultimate particles of substances. An argument, at once 
ingenious and ingenuous, for the existence of such forces is put forward 
by Lavoisier in a passage in his Elements of Chemistry which is also 
of interest for its display of the real cognitive usefulness of pre-Dalton- 
ian atomism. To Lavoisier the primitive atomic theory was a qualitative 
concept, in terms of which certain natural phenomena were more read- 
ily "understood" or construed. However, the theory lacked the definite- 
ness, the quantitative usefulness, and the more direct "evidence" with 
which Dalton subsequently endowed it. Lavoisier says: 

That every body, whether solid or fluid, is augumented in all its dimen- 
sions by any increase of its sensible heat [i.e., temperature] was long ago 

fully established as a physical axiom It is easy to perceive that the 

separation of particles by heat is a constant and general law of nature. 

When we have heated a solid body to a certain degree, and have 
thereby caused its particles to separate from each other, if we^allow the 
body to cool, its particles again approach each other , . . and, if brought 
back to the same temperature which it possessed at the commencement 

252 CASE 4 

of the experiment, it recovers exactly the same dimensions which it for- 
merly occupied. We are still very far from being able to produce the de- 
gree of absolute cold, or total deprivatioa of heat, being unacquainted 
with any degree of coldness which we cannot suppose capable of still 
further augmentation; hence it follows, that we are incapable of causing 
the ultimate particles of bodies to approach each other as near as pos- 
sible, and that these particles of bodies do not touch each other in any 
state hitherto known. Though this be a very singular conclusion, it is 
impossible to be denied. 

It may be supposed that, since the particles of bodies are thus con- 
tinually impelled by heat to separate from each other, they would have 
no connection between themselves; and that, of consequence, there could 
be no solidity in nature, unless these particles were held together by 
some other power which tended to unite them and, so to speak, to chain 
them together. This power, whatever be its cause or manner of operation, 
is named Attraction. 

Thus the particles of all bodies may be considered as subject to the 
action of two opposite powers, Repulsion and Attraction, between which 
they remain in equilibrium. So long as the attractive force remains 
stronger, the body must continue in a state of solidity; but if, on the 
contrary, heat has so far removed these particles from each other as to 
place them beyond the sphere of attraction, they lose the cohesion they 
before had with each other, and the body ceases to be solid. 

Thus, when a substance boiled, the liquid being changed to a gas, 
this was taken to signify that so much heat had been conveyed into the 
system as to overcome the cohesive forces that had previously held the 
liquid together. The striking differences in the specific heats, heats of 
vaporization, and boiling temperatures of different substances could 
be taken to indicate that different amounts of caloric fluid were re- 
quired to overcome the cohesive forces in the various cases. Conversely, 
it might be inferred that there must be considerable differences in the 
cohesive forces of different substances. From this point of view, it 
would be expected that many aspects of the behavior of solids and 
liquids should show wide variations from one material to another, 
according to the magnitude of the cohesive forces in each instance. 

In gases, on the other hand, the effects of these forces should be much 
less marked, owing to the vastly greater separation of the ultimate 
particles of gases a circumstance that profoundly reduces the inter- 
action between neighboring ultimate particles. Thus Watt's demon- 
stration that i cubic inch of water gives rise to approximately i cubic 
foot of steam indicates that, in this case, the aqueous particles are dis- 
tributed through a volume about 1700 times as great as they occupy 
in the liquid state. Gay-Lussac was thus led to expect that the behavior 
of all gases might be expressed in terms of relatively simple laws, 


while in the solid and liquid states the simple regularities would be 
partially or wholly masked by the great unsystematic variations o the 
cohesive forces in different substances. And, indeed., although the com- 
pressibilities o solids and liquids show great differences, the elastic 
behavior of all gases is closely approximated by Boyle's law; and, al- 
though the thermal expansions of solids and liquids are notably differ- 
ent from substance to substance, all gases follow Charles's law fairly 
closely. Therefore, although the relative combining volumes of liquids 
and solids showed no such simple regularity, there was still room for 
hope that, in view of the generally simpler deportment of gases, all 
gaseous reactions might display simple combining proportions analo- 
gous to that found in the hydrogen-oxygen reaction. 

Such is the line of reasoning displayed in the opening paragraph of 
Gay-Lussac's paper, and it suggests that his study of gas reactions was 
undertaken by no "happy accident," but at least in part as the conse- 
quence of a fairly sophisticated line of theoretical reasoning. Let us 
now examine Gay-Lussac's classic paper, published in 1809 in the 
Memoires de la Societe d'Arcueil^ in which he demonstrates economi- 
cally yet convincingly that there are, indeed, conspicuously simple and 
regular relationships between the combining volumes of gases. 

Memoir on the Combination of Gaseous Substances 
with Each Other 

Substances, whether in the solid, liquid, or gaseous state, possess prop- 
erties that are independent of the force of cohesion; but they also possess 
others that appear to be modified by this force (so variable in its in- 
tensity), and that no longer follow any regular law. The same pressure 
applied to all solid or liquid substances would produce a diminution 
of volume differing in each case, while it would be equal for all elastic 
fluids. Similarly, heat expands all substances; but the dilations of liquids 
and solids have hitherto presented no regularity, and it is only those of 
elastic fluids that are equal and independent of the nature of each gas. 
The attraction of the molecules in solids and liquids is, therefore, the 
cause that modifies their special properties; and it appears that it is only 
when the attraction is entirely destroyed, as in gases, that bodies under 
similar conditions obey simple and regular laws. At least, it is my inten- 
tion to make known some new properties in gases, the effects of which 
are regular, by showing that these substances combine amongst them- 
selves in very simple proportions, and that the contraction of volume 
which they experience on combination also follows a regular law. I hope 
by this means to give a proof of an idea advanced by several very dis- 
tinguished chemists that we are perhaps not far removed from the 
time when we shall be able to submit the bulk of chemical phenomena 
to calculation. 

254 CASE 4 

This statement mirrors the enormous Impact of the Newtonian 
synthesis on scientific thinking. As a result of Newton's studies of 
terrestrial and celestial mechanics, a large number of physical and 
astronomical phenomena could be understood in terms of a single 
set of laws, which could be expressed in a simple mathematical form. 

Newton's work thus unified and rationalized two broad and highly 
important domains of knowledge. It was only natural, then, that Gay- 
Lussac and many of his contemporaries should hope that chemistry 
too might soon achieve a state of similarly perfected development. 
Unfortunately this hope was not soon fulfilled; and although we can 
now construe in mathematical terms the bulk of the chemical phenom- 
ena with which Gay-Lussac was concerned, the progressively widening 
field of chemistry now comprehends vast new areas in which mathe- 
matical methods do not provide an adequate correlation of the observed 

However, although the "time when we shall be able to submit the 
bulk of chemical phenomena to calculation" was remote, the stimulus 
provided by the belief in the possibility and desirability of reaching 
such a state was a most beneficent one. It not only quickened interest 
in scientific research at large, but it particularly encouraged painstak- 
ing quantitative investigations in which accurate numerical data were 
secured, as well as the careful scrutiny of these data to discover any 
mathematically simple relations that they might contain. It was through 
such investigations that Richter, who was almost obsessed by the idea 
that chemistry could at once be made a branch of applied mathematics, 
discovered the law of reciprocal proportions; and here in Gay-Lussac's 
work we see another important and successful effort to trace a distinct 
strand of mathematically regular behavior in the tangled skein of 
reality that nature presents to the physical scientist. 

It is a very important question in itself, and one much discussed 
amongst chemists, to ascertain if compounds are formed in all sorts of 
proportions. M. Proust, who appears first to have fixed his attention on 
this subject, is of opinion that the metals are susceptible of only two 
degrees of oxidation, a minimum and a maximum; but led away by this 
seductive theory, he has seen himself forced to entertain principles con- 
trary to physics in order to reduce to two oxides all those which the 
same metal sometimes presents. M. Berthollet thinks, on the other hand 
reasoning from general considerations and his own experiments that 
compounds are always formed in very variable proportions, unless they 
are determined by special causes, such as crystallization, insolubility, or 
elasticity. Lastly, Dal ton has advanced the idea that compounds of two 
bodies are formed in such a way that one atom of the one unites with 
one, two, three, or more atoms of the other. (Dalton has been led to this 
idea by systematic considerations; and one may see from his work, A 


New System of Chemical Philosophy, p. 213, and from that of Thomson, 
Vol. 6, that his researches have no connection with mine.) It would 
follow from this mode of looking at compounds that they are formed in 
constant proportions, the existence of intermediate bodies being excluded, 
and in this respect Dalton's theory would resemble that of M. Proust; 
but M. Berthollet has already strongly opposed it in the Introduction he 
has written to Thomson's Chemistry, and we shall see that in reality it 
is not entirely exact. Such is the state of the question now under dis- 
cussion; it is still very far from receiving its solution, but I hope that the 
facts that I now proceed to set forth, facts which had entirely escaped 
the notice of chemists, will contribute to its elucidation. 

Gay-Lussac's rather neutral attitude, as here expressed, was probably 
the product of personal as well as scientific considerations. The fact 
that the present paper was published in the Memoires de la Societe 
d'Arcueil is in itself suggestive, since the Memoires was in the literal 
sense Berthollet's "house" organ. At this period, in his country house 
at Arcueil, Berthollet held frequent meetings with his friends, pupils, 
and proteges (of whom Gay-Lussac was one), and the results of these 
discussions were published in the Memoires. Under such circumstances 
it is little wonder that Gay-Lussac was disposed to view Berthollet's 
position sympathetically, especially as Berthollet's theory of affinity had 
much to recommend it. 

But it is curious that Gay-Lussac does not tell us in what sense 
Proust's contentions contravene the laws of physics nor does he indicate 
in the balance of the present paper how "we shall see that in reality it 
[i.e., Dalton's theory] is not entirely exact." On the contrary, he later 
states that he finds his own results "very favorable" to the atomic theory. 

When, in the text that follows, Gay-Lussac uses the unqualified 
expression "100 of oxygen," for example, he means 100 parts by volume 
of oxygen. It is an important indication of the different lines of ap- 
proach adopted by the two investigators that whenever Dalton uses 
the word "parts" without qualification he refers to farts by weight, 
whereas under similar circumstances in this paper Gay-Lussac always 
signifies farts by volume. Indeed, this difference may be symptomatic 
of a major difference in philosophic outlook. The British physicist 
James Clerk Maxwell suggested that there are "two modes of thinking, 
which have had their adherents in ancient and in modern times. They 
correspond to the two methods of regarding quantity the arithmet- 
ical and the geometrical. To the atomist the true method of estimating 
the quantity of matter in a body is to count the* atoms in it. The void 
spaces between the atoms count for nothing. To those who identify 
matter with extension, the volume of space occupied by a body is the 
only measure of the quantity of matter in it." 

256 CASE 4 

Gay-Lussac continues: 

Suspecting, from the exact ratio of 100 of oxygen to 200 of hydrogen, 
which M. Humboldt and I had determined for the proportions of water, 
that other gases might also combine in simple ratios, I have made the 
following experiments. I prepared fluoboric, muriatic, and carbonic gases, 
and made them combine successively with ammonia gas. 100 parts of 
muriatic gas saturate precisely 100 parts of ammonia gas, and the salt 
which is formed from them is perfectly neutral, whether one or other 
of the gases is in excess. 

That is, if 100 volumes of ammonia gas are added to 100 volumes of 
muriatic gas (hydrogen chloride), the gases disappear completely, with 
the formation of a solid salt, ammonium chloride : HCl (gas) + NH 3 
(gas) -NH 4 Cl (solid). If there is an excess of one or the other gas, 
the surplus is simply left over. Thus i 100 volumes of muriatic gas are 
added to 150 volumes of ammonia, the product will be solid ammo- 
nium chloride formed from 100 volumes each of ammonia and muriatic 
gas, and 50 volumes of unreacted ammonia gas. 

It is interesting to observe how much these experiments of Gay- 
Lussac's owe to the technical advances made in the course of 150 years' 
study of pneumatic chemistry. Such experiments, had they been con- 
ceived, could not have been performed adequately by Boyle and his 
contemporaries. The convenient collection and measurement of gases 
became possible only after Hales's deceptively simple invention of the 
pneumatic trough, first described in 1727. Much later Cavendish's 
suggestion that gases be stored over mercury led to Priestley's use of a 
pneumatic trough filled with mercury, with which he was able to 
collect and characterize several new gases, like ammonia and muriatic 
gases, which are very soluble in water. Furthermore, eudiometric (i.e., 
gas-analyzing) techniques were greatly improved by the work of 
Priestley, Cavendish, Volta, and others, so that the reactions of both 
the new and the old gases could be studied quantitatively. Hence when 
Gay-Lussac's experiments were performed the time was ripe both in 
the sense that the desirability of making such experiments was indi- 
cated, and in the sense that the laboratory tools and techniques required 
for these experiments had become available. 

Gay-Lussac next goes on to consider the combinations of carbonic 
and fiuoboric acids with ammonia. He proceeds in the same way and 
secures results of comparable simplicity, except that he finds two 
possible combinations of fluoboric acid with ammonia, and two of 
carbonic acid with ammonia, experimental conditions determining 
which one of either pair is actually obtained in a given case. These pairs 
of compounds correspond to the formation of what Gay-Lussac de- 


nominates "normal" and "sub-salts," and are reminiscent of the normal 
and acid salts discussed (page 40) in connection with Wollaston's work. 
Furthermore, when two different compounds can be formed from the 
same reactants, Gay-Lussac finds that, with a fixed volume of one gas, 
the volumes of the other gas, required to form the two compounds, 
are in the ratio i : 2. This, then, is another instance of simple multiple 
proportions and a further confirmation of Dalton's atomic theory. 

Since the particular reactions mentioned involve some relatively 
difficult chemistry and yield nothing that is essentially different from 
a number of other simpler instances that are discussed we will not 
consider Gay-Lussac's description of these experiments, on the basis of 
which he continues: 

Thus we may conclude that muriatic, fluoboric, and carbonic acids 
take exacdy their own volume of ammonia gas to form neutral salts, and 
that the last two take twice as much to form sub-salts. It is very remark- 
able to see acids so different from one another neutralize a volume of 
ammonia gas equal to their own; and from this we may suspect that if 
all acids and all alkalis could be obtained in the gaseous state, neutrality 
would result from the combination of equal volumes of acid and alkali. 
[This somewhat hasty generalization on the basis of a very few experi- 
ments is not, in fact, entirely correct.] 

It is not less remarkable that, whether we obtain a neutral salt or a 
sub-salt, their elements combine in simple ratios which may be con- 
sidered as limits to their proportions. . . 

We might even now conclude that gases combine with each other in 
very simple ratios; but I shall still give some fresh proofs. 

According to the experiments of M. Amedee Berthollet, ammonia is 
composed of 

100 of nitrogen, 
300 of hydrogen, 
by volume. . . 

The values given here, and elsewhere, by Gay-Lussac represent 
rounded figures derived from experimental data. However, here and at 
several other points in his paper, Gay-Lussac appears to overstate his 
case. Presumably he means to imply only that within the limits of 
experimental error, the figures stand in the very simple relation shown. 
In view of the acknowledged existence of experimental inaccuracies, 
such a claim would be justified; but without its important qualifying 
phrase, as used by Gay-Lussac and Dalton, it leaves a rather mistaken 
impression of either the accuracy of the experiments or the judgment 
of the investigator. 

The actual experimental results on which the figures for ammonia 
are grounded, and a brief description of the determinations by which 

258 CASE 4 

they were secured, are given in a note to the German translation of 
Gay-Lussac's paper which appeared in Gilbert's Annalen for 1810: "The 
first decomposition of ammonia was that communicated in 1785 to the 
Paris Academy by M. Berthollet. He passed electric sparks through 
ammonia gas until there was no further expansion; thereby the volume 
increased in the ratio i : 1.94117; he then examined the mixed gases in 
Volta's eudiometer, and found that they were composed of 0.725 hydro- 
gen and 0.275 nitrogen by volume. But Berthollet junior found as the 
mean of six such experiments made by him with absolutely pure am- 
monia in graduated vessels, that after absorption of the undecomposed 
gas by muriatic acid, and after the necessary corrections [for variations] 
in temperature and pressure were made (because even with a good 
electrical machine the experiment takes 6 to 8 hours at least) , the volume 
had increased in the ratio 1 12.04643 and that the gaseous mixture con- 
sisted of 0.755 hydrogen and 0.245 nitrogen by volume (but 0.755 - 2 45 
= 3.08163 : i)." Note the loose use of significant figures in this passage, 
Gay-Lussac goes on to say : 

When a mixture of 50 parts of oxygen and 100 of carbonic oxide 
(formed by the distillation of oxide of zinc with strongly calcined char- 
coal) is inflamed, these two gases are destroyed and their place taken by 
100 parts of carbonic acid gas. Consequently carbonic acid may be con- 
sidered as being composed of 

100 of carbonic oxide gas, 
50 of oxygen gas. 

[That is, carbonic oxide, prepared by the reaction ZnO + C > Zn 
+ CO, combines with half its volume of oxygen; and the product is 
carbonic acid in volume just equal to the original volume of the carbonic 
oxide alone.] 

Davy, from the analysis of various compounds of nitrogen with oxy- 
gen, has found the following proportions by weight: 

Nitrogen Oxygen 

Nitrous oxide 63.30 36.70 

Nitrous gas 44 .05 55-95 

Nitric acid 2 9-5 7-5 

Reducing these proportions to volumes we find 

Nitrogen Oxygen 

Nitrous oxide 100 49.5 

Nitrous gas 100 108.9 

Nitric acid 100 204.7 

The first and the last of these proportions differ only slightly from 
100 to 50, and 100 to 200; it is only the second which diverges somewhat 
from 100 to 100. The difference, however, is not very great, and is such 
as we might expect in experiments of this sort; and I have assured my- 
self that it is actually nil ... [This is probably an overstatement.] 


We may then admit the following numbers for the proportions by 
volume of the compounds of nitrogen with oxygen: 

Nitrogen Oxygen 

Nitrous oxide ...... 100 50 

Nitrous gas ....... 100 100 

Nitric acid ....... 100 200 

By this ingenious manipulation of data available from contemporary 
scientific literature Gay-Lussac is able to show that these figures con- 
tain a previously undetected regularity. Such a demonstration is always 
peculiarly convincing since, when the data antedate the theory and the 
experimentalist is someone other than the propounder of the theory, 
there can be no question about the data's freedom from the influences 
of conscious or unconscious desires to "validate" the theory. Of the 
many examples cited by Gay-Lussac in this paper, only a few represent 
his own experimental work; the balance are culled from previously 
published data available to everyone. 

The mechanism of the calculation in the present instance is a con- 
spicuously simple one the combining weights given by Davy are 
converted to combining volumes by the use of the gas densities (which 
we will define as weight per unit volume) of nitrogen and oxygen. 
Thus if, in a given experiment in which one of the nitrogen oxides is 
formed, w$ represents the weight of nitrogen combining with a 
weight w of oxygen, and if we let d N represent the weight per unit 
volume (the density) of nitrogen, then there participates in this re- 
action a 

weight of nitrogen participating w s 
Volume of nitrogen = 


weight or unit volume or nitrogen a y 

Furthermore, if the density of oxygen, measured under comparable 
conditions of temperature and pressure, is represented by JQ, then there 
participates a 

Volume of oxygen = -. 

Hence, for this reaction, 

TT 1 L - t W N W 

Volume of nitrogen : volume or oxygen = j : -. 

d N d 

The weights W N and w were given by Davy ; and the densities d y and 
d had been measured by Gay-Lussac's colleagues Biot and Arago, 
among others. Consequently, the ratio of the combining volumes of 

260 CASE 4 

oxygen and nitrogen were readily calculable in each case, all the data 
having been available previously. 

This type of indirect calculation was a particularly shrewd stroke in 
the present instance, because it made it possible for Gay-Lussac to draw 
inferences about the combining volumes in reactions in which the direct 
measurement of the volume ratios would have been difficult if not im- 
possible, because of various experimental problems. The process of 
indirect calculation of quantities that are not susceptible to direct 
measurement lends science the peculiar ability to reach beyond im- 
mediately attainable experience to apprehend not with certainty, but 
with some degree of probability the nature and significance of ex- 
periments that cannot be performed. 

After discussing several other examples, Gay-Lussac continues: 

Thus it appears evident to me that gases always combine in the simplest 
proportions when they act on one another; and we have seen in reality 
in all the preceding examples that the ratio of combination is i to i, i to 
2, or i to 3. It is very important to observe that in considering weights 
there is no simple and finite [integral] relation between the elements of 
any one compound; it is only when there is a second compound between 
the same elements that the new proportion of the element that has been 
added is a multiple of the first quantity. Gases, on the contrary, in what- 
ever proportions they may combine, always give rise to compounds whose 
elements by volume are multiples of each other. 

Not only, however, do gases combine in very simple proportions, as 
we have just seen, but the apparent contraction of volume which they 
experience on combination has also a simple relation to the volume of 
the gases, or at least to that of one of them. 

I have said, following M. Berthollet, that 100 parts of carbonic oxide 
gas, prepared by distilling oxide of zinc and strongly calcined charcoal, 
produce 100 parts of carbonic gas on combining with 50 of oxygen. It 
follows from this that the apparent contraction of the two gases is pre- 
cisely equal to the volume of oxygen gas added. The density of carbonic 
gas is thus equal to that of carbonic oxide gas plus half the density of 
oxygen gas; or, conversely, the density of carbonic oxide gas is equal to 
that of carbonic gas, minus half that of oxygen gas. Accordingly, taking 
the density of air as unity, we find the density of carbonic oxide gas to 
be 0.9678, rather than 0.9569, as experimentally determined by Cruik- 
shank. . . . 

Here we have another indirect calculation, but in this case the result 
can be checked against an empirical determination of the same factor, 
thus providing a valuable check on the data and the theory through 
which they are correlated. The data indicate that 

(unit volume of carbon monoxide) plus (one-half unit volume of 
oxygen) gives (unit volume of carbon dioxide), 


and inasmuch as no matter is created or destroyed in the reaction, the 

weight of the product must be the sum of the weights of the reactants. 


(weight of unit volume of carbon monoxide) + (weight of one-half 

unit volume of oxygen) = (weight of unit volume of carbon dioxide) 


(weight of unit volume of carbon monoxide) + l / 2 (weight of unit 
volume of oxygen) = (weight of unit volume of carbon dioxide) . 

Now, using the definition of density, we may write: 
(density of carbon monoxide) + l / 2 (density of oxygen) = (density 
of carbon dioxide), 


(density of carbon monoxide) = (density of carbon dioxide) 

J/2 (density of oxygen). 

Considering the relatively crude equipment and impure gases used, 
the discrepancy between the calculated value and Cruikshank's ex- 
perimental value only slightly greater than i percent is about 
as small as could be expected. 

The "densities" to which Gay-Lussac refers here and elsewhere are 
actually specific gravities, i.e., ratios of the actual densities of the gases 
to that of air, which is thus taken as a standard and assigned a "density" 
of i. 

We have seen that 100 parts of nitrogen gas take 50 parts of oxygen 
gas to form nitrous oxide, and 100 of oxygen gas to form nitrous gas. 
In the first case, the contraction is a little greater than the volume of 
oxygen added; for the specific gravity of nitrous oxide, calculated on 
this hypothesis, is 1.52092, while that given by Davy is 1.61414. But it 
is easy to show, from some of Davy's experiments, that the apparent 
contraction is precisely equal [again an overstatement] to the volume 
of oxygen gas added . . . From this circumstance, its [i.e. nitrous ox- 
ide's] specific gravity referred to that of air should be 1.52092. [This 
calculation is based upon the same line of reasoning outlined above. 
Here, however, a relatively large discrepancy, of about 6 percent, makes 
its appearance. Nevertheless Gay-Lussac, confident in the correctness of 
a generalization proved sound in so many other instances, rejects Davy's 
value as mistaken and, indeed, Gay-Lussac's figure is much more 
nearly correct.] 

The apparent contraction of the elements of nitrous gas appears, on 
the other hand, to be nil. If we admit, as I have shown, that it is com- 
posed of equal parts of oxygen and nitrogen, we find that its density, 
calculated on the assumption that there is no contraction, is 1.036, while 
that determined directly is 1.038. . . 

Ammonia gas is composed of three parts by volume of hydrogen and 
one of nitrogen, and its density compared to air is 0.596. But if we sup- 

262 CASE 4 

pose the apparent contraction to be half of the whole volume, we find 
0.594 f r tne density. Thus it is proved, by this almost perfect concord- 
ance, that the apparent contraction of its elements is precisely half the 
total volume, or rather double the volume of the nitrogen. . . 

We see, then, from these various examples, that the contraction ex- 
perienced by two gases on combination is in almost exact relation with their 
volume, or rather with the volume of one of them. Only very slight dif- 
ferences exist between the densities of compounds obtained by calcula- 
tion and those given by experiment, and it is probable that, on undertak- 
ing new researches, we shall see them vanish entirely. . . 

I shall not discuss more of these determinations, because they are only 
based on analogies, and it is besides easy to multiply them. I shall con- 
clude this Memoir by examining if compounds are formed in constant 
or variable proportions, as the experiments of which I have just given 
an account lead me to the discussion of these two opinions. 

According to Dalton's ingenious idea, that combinations are formed 
from atom to atom, the various compounds which two substances can 
form would be produced by the union of one molecule of the one with 
one molecule of the other, or with two, or with a greater number, but 
always without intermediate compounds. Thomson and Wollaston have 
indeed described experiments which appear to confirm this theory. 
Thomson has found that super-oxalate of potash contains twice as much 
acid as is necessary to saturate the alkali; and Wollaston, that the sub- 
carbonate of potash contains, on the other hand, twice as much alkali as 
is necessary to saturate the acid. 

The numerous results I have brought forward in this Memoir are 
also very favorable to the theory. But M. Berthollet, who thinks that 
combinations are made continuously, cites in proof of his opinion the 
acid sulfates, glass, alloys, mixtures of various liquids, all of which 
are compounds with very variable proportions, and he insists principally 
on the identity of the force which produces chemical compounds and 
solutions. [See Proust's statement (page 240), in which he admits that the 
same force may be responsible for both solution phenomena and chem- 
ical reactions, but points out very clearly that the action of this force is 
recognizably different in the two instances.] 

Thomson, in a letter to Dalton dated Nov. 13, 1809, writes: "In the 
second volume of the Mem. d'Arcueil which Mr. Chenevix brought 
over . . . the most important paper respecting your atomic theory is 
by Gay-Lussac. It is entirely favorable to it, and it is easy to see that 
Gay-Lussac admits it, though respect for Berthollet induces him to 
speak cautiously.'* Perhaps it was this respect for Berthollet, as well as 
the real merits of Berthollet's theory, that impelled Gay-Lussac to 
present the rather strained reconciliation of the views of Berthollet and 
Dalton that appears In the succeeding text. 

Each of these two opinions has, therefore, a large number of facts in 


its favour; but although they are apparently utterly opposed it is easy 
to reconcile them. 

We must first of all admit, with M. Berthollet, that chemical action 
is exercised indefinitely in a continuous manner between the molecules 
of substances, whatever their number and ratio may be, and that in 
general we can obtain compounds with very variable proportions. But 
then we must admit at the same time that, apart from insolubility, 
cohesion, and elasticity, which tend to produce compounds in fixed pro- 
portions, chemical action is exerted more powerfully when the ele- 
ments are in simple ratios or in multiple proportions among themselves, 
and that compounds are thus produced that separate out more easily. 
In this way we reconcile the two opinions, and maintain the great chemi- 
cal law, that whenever two substances are in presence of each other 
they act in their sphere of activity according to their masses, and give 
rise in general to compounds with very variable proportions, unless 
these proportions are determined by special circumstances. [The "great 
chemical law" was a mass-action relation by which Berthollet sought to 
construe chemical combination in terms of the gravitational forces be- 
tween reacting bodies. That is, it represented an attempt to secure a 
mathematical description of chemical phenomena by a further extension 
of the Newtonian synthesis (see page 254).] 


I have shown in this Memoir that the compounds of gaseous sub- 
stances with each other are always formed in very simple ratios, so that 
representing one of the terms by unity, the other is i, or 2, or at most 3. 
These ratios by volume are not observed with solid or liquid substances, 
nor when we consider weights, and they form a new proof that it is 
only in the gaseous state that substances are in the same circumstances 
and obey regular laws. It is remarkable to see that ammonia gas neu- 
tralises exactly its own volume of gaseous acids; and it is probable that 
if all acids and alkalies were in the elastic state, they would all combine 
in equal volumes to produce neutral salts. The capacity of saturation of 
acids and alkalies measured by volume would then be the same, and 
this might perhaps be the true manner of determining it. The apparent 
contraction of volume suffered by gases on combination Is also very simply 
related to the volume of one of them, and this property likewise is 
peculiar to gaseous substances. 

It will be noted that Gay-Lussa<:'s conclusion is a strictly factual one. 
As Berzelius observes: "M. Gay-Lussac was satisfied with having de- 
termined the ratios in which gaseous substances combine, but he made 
no wider application of this discovery." It may be that Gay-Lussac's 
cautious temperament made him disinclined to attempt a speculative 
flight on the basis of his experimental work. Whatever the reason, 

264 CASE 4 

however, he did not indicate the important bearing of the law of 
combining volumes on the apparatus of the atomic theory. 


Dalton was made aware of Gay-Lussac's work within the year 
of its publication. His first informant was probably Thomson, whose 
letter has been cited previously, and soon afterward Dalton was in 
possession of the complete text. In a letter addressed to his brother and 
dated December 1809, Dalton states that Berthollet has sent him a copy 
of the journal containing Gay-Lussac's article. Considering the then 
current state of Anglo-French relations the speed and courtesy of this 
communication are noteworthy, though apparently by no means unique. 
An even more rapid transmission of information appears to have oc- 
curred in the case of the work of Wollaston and Thomson which, 
though not published in England until 1808, is mentioned in Gay- 
Lussac's paper read late in 1808 (published in 1809). At all events, 
Dalton was familiar with Gay-Lussac's generalization by late 1809, 
and was in a position to comment on it in an appendix to the second 
part of his New System of Chemical Philosophy, which was published 
in 1810. 

In view of the new examples of simple multiple proportions and the 
generally regular behavior presented by Gay-Lussac's work, we might 
expect that Dalton, like Gay-Lussac, would view the law of combining 
volumes as "very favorable" to his atomic theory. In fact, he did not. 
He rejected this work summarily, and maintained his opposition to the 
end of his life. 

Dalton concluded, quite correctly, that Gay-Lussac's results, as in- 
terpreted by the atomic theory, strongly suggested that equal volumes 
of different gases must contain the same (or simply related) numbers 
of atoms. However, his own point of view was that there were other 
very strong indications that these numbers could be neither the same 
nor simply related to one another. Let us examine Dalton's arguments. 

The Case Against the Idea that There Are Equal Numbers of 
Particles in Equal Volumes of Different Gases. As early as 1803 (the 
year in which he first publicly intimated the existence of his atomic 
theory) Dalton wrote in his notebook: 

Though it is probable that the specific gravities of different elastic 
fluids has some relation to that of their ultimate particles, yet it is certain 
that they are not the same thing; for the ultimate particles of water or 
steam are certainly of greater specific gravity than those of oxygen, yet 
the last gas is heavier than steam. 


Here is an apparent paradox: although something with finite weight 
(hydrogen) is added to oxygen in the formation of water, the density 
of water vapor or steam is less than that of oxygen by itself. The hypoth- 
esis that different gases contain different numbers of particles per 
unit volume appears to be almost unavoidable. In itself it provides a 
satisfactory explanation, for if there are fewer particles in unit volume 
of steam than there are in unit volume of oxygen, then it is quite con- 
ceivable that the greater number of lighter particles in unit volume of 
oxygen will yield a greater density than will the smaller number of 
heavier particles in unit volume of water vapor. In entirely analogous 
fashion ammonia, formed by the addition of hydrogen to nitrogen, is 
less dense than nitrogen itself. Nor can such cases be "explained" in 
terms of conjectural buoyancy effects produced by the hydrogen. Thus, 
for example, carbon monoxide is less dense than oxygen gas, although 
the former is a compound of oxygen plus carbon. It is difficult to avoid 
the conclusion that there are fewer of these heavier carbon monoxide 
particles in unit volume of this gas than there are particles of oxygen 
in unit volume of oxygen gas; and in general such density data sug- 
gest that there are unequal numbers of particles in unit volumes of the 
various gases. 

This conclusion is powerfully supported by a scrutiny of the com- 
bining volumes in many gaseous reactions. In 1808 Dalton wrote (New 
System, page 71) : 

It is evident the number of ultimate particles or molecules in a given 
weight or volume of one gas is not the same as in another; for, if equal 
measures of azotic and oxygenous gas were mixed, and could be instantly 
united chemically, they would form nearly two measures of nitrous gas, 
having the same weight as the two original measures; but the number 
of ultimate particles could at most be one half of that before the union. 
No two elastic fluids, probably, therefore, have the same number of 
particles, either in the same volume or the same weight. 

This mode of reasoning is, apparently, impeccable. If a given volume 
of nitrogen contains n nitrogen atoms, and the same volume of oxygen 
also contains n oxygen atoms then, when these gases are mixed we 
have 2 volumes of a mixed gas containing a total of in atoms. When 
the oxygen and nitrogen combine there appears to be little volume 
change, and the product is approximately 2 volumes of nitrous gas. 
But now, even if the simplest formula is assigned to the molecule of 
nitrous gas that is, one atom of nitrogen an'd one atom of oxygen 
it is plain that from the 2/2 atoms originally present only n molecules 
of nitrous gas can result. Consequently, since the nitrous gas contains 
only n particles in 2 volumes, while the nitrogen and oxygen were each 

266 CASE 4 

assumed to contain n particles in i volume, the nitrous gas can contain 
no more than half as many particles per unit volume as do nitrogen and 

Some illustration of this relation may be of value. Suppose we have 
a (very small) unit volume of nitrogen, containing just 1,000 nitrogen 
atoms. We will suppose that an equal volume of oxygen contains 1,000 
oxygen atoms. When the gases are mixed, and made to react, it appears 
that no more than 1,000 molecules of nitrous gas could be obtained. 
But experiment shows that two unit volumes of this gas are formed. 
Therefore it seems that each unit volume of nitrous gas contains but 
500 molecules, or only half as many "particles" as were supposed to be 
present in an equal volume of nitrogen or oxygen. 

This is but one of a number of similar cases with which Dalton was 
familiar. Thus the combining volumes in the following reactions were 
known to be roughly as stated below even before Gay-Lussac indicated 
that they were almost exactly as shown; 

i volume nitrogen + 3 volumes hydrogen 2 volumes ammonia, 
i volume oxygen + 2 volumes hydrogen - 2 volumes water vapor. 
In the first case it is plain that if n atoms of nitrogen are present in 
unit volume of nitrogen gas, we can secure from it no more than n 
molecules of ammonia, each containing one nitrogen atom. However, 
since two volumes of ammonia are produced, the number of molecules 
in each of these volumes of this gas must be w/2, or only half as great 
as the number of nitrogen particles in unit volume of that gas. An 
analogous line of reasoning indicates that the number of molecules of 
water vapor in unit volume of steam can be only half as great as the 
number of oxygen atoms in unit volume of oxygen. And in general, 
in any case in which the volume of a gaseous reaction product exceeds 
the volume of one of the reacting gases, there is a strong indication 
that there are fewer particles in unit volume of the product than there 
are in an equal volume of the reacting gas. Thus the conclusion that 
there are different numbers of particles in equal volumes of different 
gases was powerfully supported by experimental data on gaseous densi- 
ties and combining volumes in gaseous reactions. 

Dalton was also able to show that this conclusion was consistent 
with one of his previous suppositions. Believing as he did (see page 225) 
that the particles of an elastic fluid were in direct contact with one an- 
other, through their heat atmospheres, Dalton had the following con- 
ception of the structure of a gas: 

When we contemplate upon the disposition of the globular particles 
in a volume of pure elastic fluid, we perceive it must be analogous to 
that of a square pile of shot; the particles must be disposed into horizontal 


strata, each four particles forming a square: in a superior stratum, each 
particle rests upon four particles below. 

However, if the space ocupied by all gases is uniformly and tightly 
packed with the particles of the various gases, and if, as suggested above, 
different numbers of particles suffice to fill the same volume of differ- 
ent gases then there appears to be no alternative to the belief chat 
the different gaseous particles occupy different volumes, and hence have 
different diameters. This is the view adopted by Dalton (New System, 

At the time I formed the theory of mixed gases, I had a confused idea, 
as many have, I suppose, at this time, that the particles of elastic fluids 
are all of the same size; that a given volume of oxygenous gas contains 
just as many particles as the same volume of hydrogenous; or if not, 
that we had no data from which the question could be solved. But from 
a train of reasoning, similar to that exhibited at page 71 [see page 265], 
I became convinced that different gases have not their particles of the 
same size: and that the following may be adopted as a maxim, till some 
reason appears to the contrary: namely, 

That every species of pure elastic fluid has its particles globular and all 
of a size; but that no two species agree In the size of their particles, the 
pressure and temperature being the same. 

This conclusion is in the most gratifying agreement with a conclu- 
sion previously adopted (page 226) by Dalton : namely, that the homo- 
geneity of a complex atmosphere was maintained by a mechanism 
depending on the existence of differences in the effective diameters of 
the various constituent gases. 

Not content with the conclusion that the particle diameters were 
unequal in different gases, Dalton proceeded to derive numerical values 
for the relative diameters of the particles of the different gaseous 
species. We need not consider the details of this computation, which 
was based on the solid geometry of a pile of shot and made use of 
the measured gas densities and the atomic and molecular weights de- 
termined from chemical data. Owing to the errors in the primary 
experimental data and the misconceptions involved in their interpreta- 
tion, Dalton found, quite in accord with his expectations, that the par- 
ticle diameters (and volumes) were usually different in the various 
elastic fluids for which the calculations were made. To be sure, in a 
few cases he did find equal diameters for the particles of different gases, 
but he apparently considered them as no more than accidental approxi- 
mations to the same diameter, rather than as precisely equal diameters. 
In any event, he saw in them no essential contradiction o the maxim 

268 CASE 4 

enunciated in the last-quoted passage; on the contrary, he was much 
impressed by the striking differences in the calculated diameters of 
the particles of the large majority of the gaseous species considered. 

The further significance of this computation lay in its intimation 
that in equal volumes of different gases, tightly packed with particles 
of different sizes, the relative numbers of particles must be unequal 
Most important of all, the calculated values of these relative numbers 
were not related in any simple way. 

Dalton Rejects the Law of Combining Volumes as an Exact Portrayal 
of Phenomena, but Infer entially Accepts and Uses It as an Approxima- 
tion. Although the evidence outlined above appears to be decisive, the 
conclusion to which it leads is the very antithesis of the import of 
Gay-Lussac's generalization, as interpreted by the atomic theory. If we 
admit, with Gay-Lussac, that the combining volumes of different gases 
are always in the ratio of small whole numbers, and if as postulated 
by the atomic theory a molecule of a compound is always formed 
from a small number of atoms, then equal volumes of different gases 
must contain numbers of their respective atoms that are either equal 
or in the ratio of small whole numbers. Thus, for example, when Gay- 
Lussac asserted that equal volumes of nitrogen and oxygen combined 
to form nitrous gas (each molecule of which was rightly believed to 
contain one atom of oxygen and one atom of nitrogen) the unavoidable 
implication was that the equal volumes of these two gases contained 
exactly equal numbers of their respective atoms. But according to Dai- 
ton's calculations the relative numbers of atoms of oxygen and nitro- 
gen in equal volumes of the respective gases stood in the ratio i : 0.833. 
Consequently the combining volumes of oxygen and nitrogen should 
be in the ratio 0.833 : *> to which the i : i ratio asserted by Gay-Lussac 
is only a crude approximation. Examination of the other instances dis- 
cussed by Gay-Lussac brought to light a multitude of similar anomalies, 
and Dalton, very naturally, came to believe that Gay-Lussac had grossly 
oversimplified what were actually nonintegral ratios. And indeed, as 
we have already observed (page 257), Gay-Lussac never did secure pre- 
cisely integral volume ratios directly from his empirical data, but only 
obtained them by rounding off volume ratios that were more or less 
close approximations to simple integral ratios. Thus Dalton must have 
felt every confidence in his position when, in 1810, he wrote: 

Some observations on nitric acid, 'and the other compounds of azote 
and oxygen, have been made by Gay-Lussac, in the 2d. vol. of the 
Memoires d'Arcueil. He contends that one measure of oxygenous gas 
unites to two measures of nitrous gas to form nitric acid, and to three 
measures to form nitrous acid. Now I have shewn that i measure of oxy- 
gen may be combined with 1.3 of nitrous gas, or with 3.5, or with any 


intermediate quantity whatever, according to circumstances, 5 which he 
seems to allow; what, then, is the nature of the combinations below 2, 
and above 3, of nitrous gas? No answer is given to this; but the opinion 
is founded upon an hypothesis that all elastic fluids combine in equal 
measures, or in measures that have some simple relation one to another, 
as i to 2, i to 3, 2 to 3, etc. In fact, his notion of measures is analogous 
to mine of atoms; and if it could be proved that all elastic fluids have 
the same number of atoms in the same volume, or numbers that are as 
i, 2, 3, etc. the two hypotheses would be the same, except that mine is 
universal, and his applies only to elastic fluids. Gay-Lussac could not 
but see ... [see page 267] that a similar hypothesis had been enter- 
tained by me, and abandoned as untenable; however, as he has revived 
the notion, I shall make a few observations upon it, though I do not 
doubt but he will soon see its inadequacy. 

After this rather patronizing introduction Dalton goes on to attack 
the accuracy of Gay-Lussac's data, as well as his interpretations of 
them. However, while it is quite true that Gay-Lussac's generalization 
was only suggested (rather than "proved") by the relatively inaccurate 
data available to him, Dalton's criticism is not without an element of 
unconscious humor, since he had himself, on numerous occasions, 
accepted even less striking approximations as quite satisfactory "veri- 
fication" of his own atomic theory. In the same book from which the 
preceding passage is taken we find him writing that in considering 
the compounds of oxygen with azote: 

Our plan requires a ... principle of arrangement; namely, to begin 
with that which is most simple, or which consists of the smallest number 
of elementary particles, which is commonly a binary compound, and 
then to proceed to the ternary and other higher compounds. According 
to this principle, it becomes necessary to ascertain, if possible, whether 
any of the [compounds], and which of them, is a binary compound. As 
far as the specific gravities of the two simple gases are indicative of the 
weights of their atoms, we should conclude that an atom of azote is to 
one of oxygen as 6 to 7 nearly; the relative weights of ammonia and 
water also give countenance to such a ratio. 

Although Dalton had previously established to his own satisfaction 
(see the preceding extract) that the numbers of particles in equal 

5 Dalton is quite right in asserting the wide variability of the combining proportions 
of nitrous air and oxygen. As already remarked, the nitrous air test is not reliable because 
the exact course of the reaction is too sensitive to small changes in the experimental condi- 
tions. According to whether these conditions favor formation of NO 2 (NO + O) N 2 Oa 
(2NO -+- O) in greater or smaller proportion, the reacting volumes are continuously varia- 
ble between fixed extremes. Owing to various experimental aberrations the extremes de- 
fined by Gay-Lussac (2 nitrous gas to i oxygen, and 3 nitrous gas to i oxygen), which 
readily allow for the possibility of combining proportions between 2 to i and 3 to i, 
did not agree with the limits determined by Dalton as 1.3 and 3.5 of nitrous air to i of 
oxygen, according to the conditions. 

270 CASE 4 

volumes of different gases could not be equal, he here embarks upon 
a calculation of relative atomic weights which is based on the assump- 
tion that the numbers are at least approximately equal. If there is 
almost the same number n of atoms in unit volumes of azote and oxy- 
gen, and if a and o represent the weights of atoms of azote and oxygen, 
respectively, then the total weights of azote and oxygen in unit volumes 
of each must be n X a and n X o, respectively. The ratio of the specific 
gravities of azote and oxygen, given by Dalton as 6:7, must be the 
same as the ratio of the respective densities. Hence: 

Specific gravity of azote ___ 6 __ Density of azote 
Specific gravity of oxygen 7 Density of oxygen 

Density of azote _ Weight of unit volume of azote 

Density of oxygen Weight of unit volume of oxygen 




Consequently the atomic weights stand in the same ratio as, and may 
be calculated from, the ratio of the specific gravities or densities. That 
is, the atomic weights stand in the ratio of 6 : 7. 

These figures were consistent with the atomic weights calculated 
from the combining weights of the elements in ammonia and water, 
when the molecular formulas were taken to be NH and HO respec- 
tively, as predicted by the rule of greatest simplicity. Such concordance 
was reassuring, but was attainable only by the use of an assumption 
that Dalton had previously rejected that there are equal numbers of 
atoms in equal volumes of the gaseous elements. Indeed, Dalton did 
not hesitate to attack Gay-Lussac's work vigorously when the very 
same assumption appeared to be justified as a logical deduction from 
that work. The distinction suggested by Dalton's use of this assumption 
is that, though he would not regard it as exact, he did accept and use 
it as a serviceable approximation. Dalton was very explicit in indicating 
the provisional nature of his calculation "as far as the specific 
gravities of the two simple gases are indicative of the weights of their 
atoms . . ." thus signifying that the basic assumption was enter- 
tained only as a provisional approximation, rather than as a mathe- 
matically exact relation. The values he then secured proved to be in 
good agreement with those obtained from an independent calculation 
based on the combining weights of the elements in ammonia and 


water. This concordance served to justify the use of the assumption as 
a provisional approximation. 

But the best criterion is derived from a comparison of the specific gravi- 
ties of the compound gases themselves. Nitrous gas has the least specific 
gravity of any of them; this indicates it to be a binary compound; nitrous 
oxide and [nitric] acid are both much heavier; this indicates them to be 
ternary compounds; and the latter being heavier than the former, indi- 
cates that oxygen is heavier than azote, as oxygen is known to abound 
most in the latter. 

Dalton again makes use of an assumption like that mentioned in the 
previous text. He accepts the relative magnitudes of the compounds' 
specific gravities as "the best criterion" for the assignment of their 
respective molecular formulas. This implies the risky assumption that 
there are equal numbers of molecules in equal volumes of the com- 
pound gases; but even if these numbers are only roughly the same, the 
specific gravities provide a sufficiently good indication of the relative 
magnitudes of the molecular weights to make it possible to distinguish 
the binary from the ternary compounds, for example. 

Now, of all the compounds containing only azote and oxygen, 
nitrous gas has by far the smallest specific gravity. If the numbers of 
molecules in equal volumes of the compound gases are even approxi- 
mately the same, we might then be justified in concluding that the gas 
with the least specific gravity must be the material with the lightest 
molecules, i.e., that it is the binary compound, containing one atom of 
oxygen and one of azote. Hence, the formula of the binary compound, 
NO, may be provisionally assigned to nitrous gas. The next heavier 
oxides of azote, nitrous oxide and nitric acid, have much larger specific 
gravities, that of nitric acid being the greater. This indicates that they 
are the ternary compounds, N 2 O and NO 2 . It was known that, of these 
two substances, nitric acid was the richer in oxygen. Hence the formula 
NO 2 could be assigned to it, leaving N 2 O as the formula of nitrous 
oxide. The slightly greater specific gravity of the nitric acid (in which 
one of the azote atoms in nitrous oxide is replaced with an oxygen 
atom) is in harmony with the previously developed evidence (see 
page 270) that the atomic weight of oxygen is slightly greater than that 
of azote. 

It should be observed that this assignment of molecular formulas is 
a conspicuously reasonable one, and that the assumption on which it 
rests need only be accurate enough to show the relative orders of mag- 
nitude of the various molecular weights. However, since there is still 
no assurance that it is sound enough even for that purpose, the molec- 
ular formulas derived from it have only a provisional status. Fortu- 

272 CASE 4 

nately, Dalton was able to develop strong evidence for the validity of 
these formulas. He presents this evidence in the form of a table ob- 
tained by treating an entirely different set of data by an independent 
interpretive procedure. 

Let us now see how far the facts already known will corroborate these 

According to Cavendish and Davy, who are the best authorities we 
yet have in regard to these compounds, they are constituted as under. 
[See Table i.] 

The above table is principally taken from Davy's Researches: where 
two or more results are given under one article, they are derived from 
different modes of analysis In the third column are given the ratios of 
the weights of azote and L ygen in each compound, derived from the 
preceding column, and reduced to the determined weight of an atom of 
oxygen 7. This table corroborates the theoretic views above stated most 
remarkably. The weight o' an atom of azote appears to be between 
5.4 and 6.1: and it is worthy of notice, that the theory does not differ 
more from the experiments than they differ from one another; or, in 

TABLE i. Dalton's table of weight ratios of nitrogen oxides 

[Compound] Sp. gr. Constitution by weight Ratios * 

Nitrous gas 

1. 102 46.6 azote 

+ 53-4 oxygen 





+ 55-8 




+ 57-7 




Nitrous oxide 

1.614 63-5 

+ 36.5 

2X 6.1 



+ 08 

2 y 5.7 


~ j u 

/\ J / 



, I 2Q 

2 X 54 


Nitric acid 

2-444 29.5 

+ 70-5 



7X2 . 



+ 70-4 





+ 72 

e j 



/ /\ * 


+ 74-7 


7X2 ^ 

* If we take a as the atomic weight of azote and o as the atomic weight of oxygen, 
then, if the provisional formulas are correct, the weight ratios of the elements in the 
various nitrogen oxides should be: 

Compound Weight of azote : Weight of oxygen 

NO a : o 

N 2 O 2 X * * o 

NO a a : o X * 

Dalton calculates these weight ratios from the tabulated analytic data of Cavendish and 
Davy. For o, the atomic weight of oxygen, he uses the figure 7 (deduced from the com- 
bining weights of the elements in water) and he computes the corresponding value of a 
in each case. If the atomic theory were correct, and if the molecular formulas were cor- 
rectly assigned, then we would expect to find that a is a constant in the neighborhood of 6", 
since it has previously been indicated (see page 270) that the atomic weights of azote and 
oxygen stand approximately in the ratio 6:7. 


other words, the mean weight of an atom of azote derived from the 
above experiments would equally accommodate the theory and the ex- 
periments . . . 

I have been solicitous to exhibit this view of the compounds of azote 
and oxygen, as derived from the experience of others, rather than from 
my own; because, not having had any views at all similar to mine, the 
authors could not have favoured them by deducing the above results, if 
they had not been conformable to actual observation. 

Dalton expresses his satisfaction with th^ results of his calculation 
"this table corroborates the theoretic views above stated most remark- 
ably." Yet, although the (italicized) figu es for the atomic weight of 
azote approximate a constant, as they shcpd, the range is fairly broad, 
from 4.7 to 6.1 (not 5.4 to 6.1, as stated by Dalton). But Dalton, guided 
by the precepts of his theory, perceives th^t these figures are sufficiently 
close to a constant to serve as "confirmation" of the atomic theory; and 
he feels, quite correctly, that the observed variability is no greater than 
is to be anticipated as a result of the inaccuracies of the primary data. 

Compare with this Dalton's appraisal of Gay-Lussac's interpretation 
of the same data. Dalton denies the validity of volume relations that 
approximate their ideal values as well as do the deductions he had him- 
self drawn from the same analyses. Furthermore, while he confidently 
assumes that improved analyses will lend even stronger support to his 
own theory, he suggests that if better data were available they would 
not support Gay-Lussac's interpretation. The origin o Dalton's diverse 
appraisals is fairly apparent: in one case his theory taught him to expect 
and recognize certain regularities; in the other case it taught him that 
no regularities could exist, and impelled him to deny any such regu- 
larities although they were no less apparent than those that he discerned 
for himself. A theory or conceptual scheme thus acts as a two-edged 
weapon, and it appears probable that Dalton's situation at this juncture 
was much like that which he rather smugly attributes to some of his 
contemporaries : 

When the mind is ardently engaged in prosecuting experimental en- 
quiries, of a new and extraordinary kind, it is not to be expected that 
new theoretic views can be examined in all their relations, and formed 
so as to be consistent with all the well known and established facts of 
chemistry; nor that the facts themselves can be ascertained with that 
precision which long experience, an acquaintance with the instruments, 
and the defects to which they are liable, and a comparison of like obser- 
vations made by different persons, are calculated to produce. This may 
appear to be a sufficient apology for the differences observed in the 
results of ... celebrated chemists, and for the opposition, and some- 
times extravagance, of their views. 

274 CASE 4 

The extravagance o Dalton's own view is expressed in his forthright 
rejection of Gay-Lussac's generalization: 

The truth is, I believe, that gases do not unite in equal or exact meas- 
ures [integral ratios] in any one instance; when they appear to do so, it 
is owing to the inaccuracy of our experiments. In no case, perhaps, is 
there a nearer approach to mathematical exactness, than in that of i 
measure of oxygen to 2 of hydrogen; but here, the most exact experi- 
ments I have ever made, gave 1.97 hydrogen to i oxygen. 

It is a little amusing to observe Dalton, whose experiments were gen- 
erally very crude, quoting his own values as a refutation of those of 
Gay-Lussac, who was an acknowledged experimental virtuoso. Had 
this been an instance where Dalton would have expected to find a 
simple i : 2 ratio he would certainly have accepted i : i .97 as a very 
satisfactory check. Here, however, armed with the staff of his theory, 
he enjoyed full confidence that Gay-Lussac could not be right, and the 
deficiency of 1.5 percent assumed a very large importance in his eyes. 

We possess an interesting exchange of letters between Dalton and 
Berzelius. Writing in 1812 Dalton reiterates his position: 

The French doctrine of equal measures of gases combining, etc., is 
what I do not admit, understanding it in a mathematical sense. At the 
same time I acknowledge there is something wonderful in the frequency 
of the approximation. 

The doctrine of [multiple] proportions appears to me mysterious 
unless we adopt the atomic hypothesis. It appears like the mystical ratios 
of Kepler, which Newton so happily elucidated. [Kepler had shown that 
the movements of the planets could be correlated in terms of several 
simple mathematical relations. These he derived from purely observa- 
tional data, in the interpretation of which he was, however, guided by 
his firm belief in Pythagorean-Platonic number mysticism. The "real" 
reasons for the existence of the simple relations discovered by Kepler 
remained entirely obscure until Newton showed that they could be 
deduced from, and understood in terms of, the action of universal gravi- 
tation.] The prosecution of the investigation can terminate, I conceive, 
in nothing but in the system which I adopt of particle applied to particle. 

To this Berzelius responded with full appreciation of Dalton's accom- 
plishments, but without disguising his opinion that Dalton had adopted 
an unreasonable attitude with regard to Gay-Lussac's work. 

I believe that it is necessary to let experiment mature the theory. If 
the latter begins to concern itself with constraining nature into certain 
forms, the theory will stop growing toward perfection and will cease to 
be useful. [This is a handy stick with which to beat an opposing point 
of view. However it should be noted that when his own profoundest 


scientific convictions were involved, Berzelius did not hesitate to "force" 
the facts into conformity with his theories, and in this respect he did no 
more than a number of other brilliant investigators.] I agree that the 
theory of multiple proportions is a mystery but for the Atomic Hypoth- 
esis, and as far as I have been able to judge, all the results so far obtained 
have contributed to justify this hypothesis. 

I believe, however, that there are parts of the general theory, for which 
science is indebted to you, which require some slight alteration. That part, 
for example, which induces you to declare inexact the experiments of 
Gay-Lussac on the combining volumes of gases. I should have thought 
that these experiments were the finest proof of the probability of the 
atomic theory, and, moreover, I cannot so easily believe that Gay-Lussac 
is mistaken, especially in a matter where it is only a question of meas- 
uring well or badly. 

Berzelius suggests here that there is nothing conjectural about Gay- 
Lussac's results; as experimental values derived by a gifted investigator 
they lay claim to the status of "brute facts." Berzelius' injunction was, 
however, disregarded by Dalton who, seeing no way of reconciling his 
theory with the alleged facts, continued to deny the validity of the facts. 
However, with the passage of time, the evidence for the facts ulti- 
mately became conclusive, and the reconciliation of the theory and the 
facts became a matter of more crucial importance. Possible roads to such 
a reconciliation will be discussed in succeeding sections. 


The Italian physicist Avogadro suggested a highly ingenious 
method for the mutual reconciliation of the atomic theory and Gay- 
Lussac's law of combining volumes, but before we examine the details 
of Avogadro J s proposal, it will be well to review the contradiction that 
seemed so irreconcilable to Dalton. 

First then, we must allow that Gay-Lussac's law of combining vol- 
umes, as interpreted by the atomic theory, strongly suggests that in 
equal volumes of different gases the numbers of the respective gaseous 
particles are either equal or simple (integral) multiples of one another. 
One such derivation has already been suggested (page 268) and might 
run: if the formula of nitrous gas is NO, the formation of this sub- 
stance will always require equal numbers of nitrogen and oxygen 
atoms. Gay-Lussac asserted that under the same conditions of tempera- 
ture and pressure the volumes of oxygen and nitrogen that reacted 
with each other to form nitrous gas were precisely equal. Thus it is 
plain that at equal temperatures and pressures there must be equal 
numbers of the respective atoms in equal volumes of oxygen and 

276 CASE 4 

(1) There are a number of chemical reactions in which the volume 
of a gaseous product exceeds the volume of at least one of the reacting 
gases. Among these cases we may note: 

i volume of oxygen + carbon (solid) 

2 volumes of carbon monoxide (CO), 

i volume of oxygen + i volume of nitrogen 

-2 volumes of nitrous gas (NO), 

i volume of oxygen + 2 volumes of hydrogen 

-2 volumes of water vapor (H 2 O). 

In the first instance, for example, if we allow that each molecule of 
carbon monoxide must contain at least one oxygen atom, then it is 
plain that the two volumes of carbon monoxide can contain only as 
many molecules as there are atoms of oxygen in the one volume of 
oxygen. It would appear, then, that there are only half as many particles 
(molecules) in a given volume of carbon monoxide as there are particles 
(atoms) in an equal volume of oxygen. There is one rather implausible- 
looking way in which the "equal volumes equal numbers" idea can 
be salvaged in such instances. If we were to assume that there occurred 
something essentially impossible under Dalton's definition of an atom 
namely, that the oxygen atom was split into two identical fragments 
then we would have twice as many of these oxygenous fragments as 
there were atoms of oxygen to begin with. If each carbon monoxide 
molecule contained just one of these fragments, then we could have 
twice as many molecules of carbon monoxide as we had atoms of 
oxygen, and the fact that the volume of the carbon monoxide is twice 
as great as that of the oxygen is made consistent with the "equal vol- 
umes-equal numbers" scheme. In the same way, by allowing the 
splitting of the oxygen atom, that scheme can also be maintained in 
the other instances cited. 

However, this consistency is dearly bought at the price of postu- 
lating an occurrence repugnant to one of the definitions of the atomic 
theory. (Note, once again, that the Greek "atomos" means uncut, 
indivisible.) This price seemed inordinately high to Dalton, and he 
preferred to abandon the speculative "equal volumes-equal numbers" 
argument that exacted it. He concluded that there simply were sub- 
stantially fewer particles in a given volume of nitrous gas, or of water 
vapor, or of carbon monoxide, than there were in an equal volume of 

(2) Several anomalies in the measured gaseous densities seemed to 
lend color to this view. Thus the densities of water vapor (oxygen 
plus hydrogen) and of carbon monoxide (oxygen plus carbon) are 
less than that of oxygen itself, though in each case something has been 
added to the oxygen. That the individual molecules of carbon monoxide 


must be heavier than the oxygen particles appears evident, and when 
this proposition is combined with the observed gaseous densities, we 
seem to be led inescapably to the conclusion that there are fewer par- 
ticles in a volume of carbon monoxide or water vapor than there are in 
an equal volume of oxygen. This conclusion is in good agreement with 
Dalton J s provisional interpretation of item (i). 

(3) Dalton's meteorological considerations had led him to believe 
that the particles of different gases were of different diameters (see 
page 20). If we accept the Daltonian conception of a gas as solidly 
packed with particles, like a pile of shot, it is plain that, except in a few 
fortuitous cases, equal volumes of gases containing particles of different 
size could not well contain equal numbers of these particles. 

(4) If we accept the analogy between a volume of gas and a container 
full of shot, then we must also admit the pertinence of Dalton's calcu- 
lation, from gas-density and atomic-weight data, of the relative numbers 
of particles present in different gases. The results of the calculations 
indicated that, by and large, these numbers were significantly different, 
and not simply related to one another. 

(5) Dalton asserted, quite correctly, that the experimental figures of 
Gay-Lussac, and the figures that the latter calculated from the experi- 
ments of others, supported the law of combining volumes relatively 
weakly, because these figures had to be rounded off more or less 
arbitrarily before the data and the "law" could be brought into agree- 
ment. To Gay-Lussac this rounding off was a legitimate operation that 
simply took cognizance of the existence of substantial experimental 
errors in the data used; to Dalton it was, as we have seen in the last 
Section, an unacceptably gross oversimplification of these data. 

Not all of these five points are equally crucial. Thus, for example, 
argument (5) gradually lost its force as subsequent investigations pro- 
vided more precise confirmation of the very simple combining propor- 
tions postulated by Gay-Lussac. Furthermore, the significance attaching 
to points (3) and (4) is directly dependent on the degree of acceptance 
accorded to the Daltonian (pile-of-shot) model of a gas. This was, of 
course, a strictly hypothetical conception, without any direct "proof," 
and as time went on there was a gradual accumulation of opinion and 
evidence against it. Thus, if the Daltonian model is not accepted, and 
a gas is viewed as a space only thinly populated with particles, there 
ceases to be any direct and compelling connection between the particle 
diameters and the numbers of these particles present. 

We have still to deal with points (i) and (2), and these cannot be 
dismissed lightly. They do not in themselves exclude the idea that the 
numbers of particles in equal volumes of different gases are simply 
related to one another. (Thus, for example, the assumption that there 

278 CASE 4 

are twice as many particles in unit volume of oxygen as there are in 
unit volumes of carbon monoxide, or nitrous gas, or water vapor meets 
with no serious contradiction.) But it does appear that the observations 
embodied in these points rule out the possibility that there are equal 
numbers of particles in equal volumes of different gases. This is the 
crux of the matter with which Avogadro concerns himself, and we may 
now address ourselves to a consideration of his work. 

Avogadrds Proposals. Avogadro, an Italian physicist, published his 
celebrated paper in the French Journal dc Physique, in 1811. The French 
text suffers from occasional obscurity, which must have confused 
Avogadro's contemporaries even as it does us. The situation was further 
beclouded by the fact that in his text Avogadro does not make a clear 
distinction between atoms and molecules, though he apparently dis- 
tinguished them clearly in his thinking. He abjures the use of the word 
"atom" and, just as we have used the word "particle" (from the Latin 
for "small part") to denote any minute body, so he uses the word 
"molecule" (from the Latin for "small mass") with various qualifying 
adjectives. He is fairly consistent in employing these terms and quali- 
fications in the following senses: molecule (unqualified) signifies any 
small particle, atom or molecule; integral (or composite or compound) 
molecule usually signifies a molecule of a compound, though it is occa- 
sionally used in the sense of a molecule of any sort; constituent molecule 
means the molecule of an element; elementary molecule means the 
atom of an element. 

Extracts from Avogadro's paper follow. 

Essay on a Manner of Determining the Relative Masses of the Elementary 

Molecules of Bodies, and the Proportions in which They 

Enter into These Compounds 


M. Gay-Lussac has shown in an interesting Memoir that gases always 
unite in a very simple proportion by volume, and that when the result of 
the union is a gas, its volume also is very simply related to those of its 
components. But the proportions by weight of substances in compounds 
seem only to depend on the relative number of molecules which com- 
bine, and on the number of compound molecules which result. It must 
then be admitted that very simple relations also exist between the vol- 
umes of gaseous substances and the numbers of simple or compound 
molecules which form them. The first hypothesis to present itself in this 
connection, and apparently even the only admissible one, is the supposi- 
tion that the number of integral molecules in any gas is always the same 
for equal volumes, or always proportional to the volumes. 

The reasoning on which Avogadro founded this statement was 
probably based, at least in part, on an algebraic argument which we 


need not here consider. This treatment indicates that the numbers of 
particles in equal volumes of different gases are simply (integrally) 
related. This is not at all the same as saying that the numbers are 
equal, which is merely the simplest possible (one-to-one) integral re- 
lation. However, lacking any clear criterion for deciding just what the 
relations actually were, Avogadro wisely declared in favor of the pro- 
visional adoption of the simplest possible one. This relation is quite 
promising. As we have already seen, it goes far toward explaining the 
existence of the law of combining volumes. Furthermore, as Avogadro 
points out in his next sentence, it is so simple that any special postu- 
lates, about "the law regulating the distances" between the particles, 
are unnecessary. Presumably by this "law" he means a relation such as 
that shown by Newton to describe the relative positions of the bodies 
of the solar system. 

His emphasis on the "equal volumes-equal numbers" idea is one of 
Avogadro's two major contributions. There is, of course, little that is 
new in this hypothesis; more than fifty years earlier it had been enter- 
tained by Bernoulli, and we have seen (page 265) that it was both 
recognized and rejected by Dalton. However, Avogadro now goes on 
to display the extraordinary value of this idea; and, at the same time, 
he is able to show that some of the theoretical difficulties which its 
acceptance seemed to entail are not nearly as disastrous as they were 
thought to be by Dalton. 

Indeed, if we were to suppose that the number of molecules contained 
in a given volume were different for different gases, it would scarcely be 
possible to conceive that the law regulating the distance of molecules 
could give in all cases relations as simple as those which the facts just 
detailed compel us to acknowledge between the volume and the number 
of molecules. On the other hand, it is very well conceivable that the 
molecules of gases being at such a distance that their mutual attraction 
cannot be exercised, their varying attraction for caloric may be limited 
to condensing a greater or smaller quantity around them, without the 
atmosphere formed by this fluid having any greater extent in the one 
case than in the other, and, consequently, without the distance between 
the molecules varying; or, in other words, without the number of mole- 
cules contained in a given volume being different . . . But in our present 
ignorance of the manner in which this attraction of the molecules for 
caloric is exerted ... we should rather be inclined to adopt a neutral 
hypothesis, which would make the distance between the molecules and 
the quantities of caloric vary according to unknown laws, were it not 
that the hypothesis we have just proposed is based on that simplicity of 
relation between the volumes of gases on combination, which would 
appear to be otherwise inexplicable. 
The argument here invoked by Avogadro is strongly reminiscent of 

280 CASE 4 

that advanced by Gay-Lussac (see page 253) in explanation of the gen- 
erally simple behavior of gases, that is, the distances between individual 
gaseous particles are assumed to be so great in comparison with their 
diameters that the variable attractive forces between neighboring par- 
ticles are negligible. Avogadro suggests that under such circumstances 
the various quantities of caloric fluid held by the particles of different 
gases do not significantly influence the effective particle diameters, so 
that this fluid may be present in different amounts "without the distance 
between the particles varying; or, in other words, without the number 
of molecules contained in a given volume being different." While 
Avogadro says explicitly that he knows of no absolute criterion for the 
estimation of relative particle diameters, interparticle separations, or 
particle numbers in equal volumes of different gases, he emphasizes 
that the hypothesis of equal effective diameters squares well with Gay- 
Lussac's law, while Dalton's assumption of characteristically different 
diameters does not. 

A few years after Avogadro's publication, the French physicist 
Ampere arrived independently at the same conclusion that equal 
volumes of different gases contain the same number of particles. In this 
case the effect of differences in the various particle diameters was en- 
tirely ignored, apparently because Ampere felt that the distances between 
individual gaseous particles were so great that the unequal diameters 
of the particles would have no substantial effect on the volumes of 
different gases that contained equal numbers of these particles. Ampere's 
statement on this point is so clearly and thoughtfully presented that it 
is worth while to examine it here. 

When bodies pass into the gaseous state, their several particles are 
separated by the expansive force of heat to much greater distances from 
each other than when the forces of cohesion or attraction exercise an 
appreciable influence; so that these distances depend entirely on the 
temperature and pressure to which the gas is subjected, and under equal 
conditions of temperature and pressure the particles of all gases, whether 
simple or compound, are equidistant from each other. The number of 
particles is, on this supposition, proportional to the volumes of the gases. 
Whatever be the theoretical reasons which, in my opinion, support the 
above conclusion, it cannot be considered as anything but an hypothesis. 
But if, on comparing the inferences which follow from it as necessary 
consequences with the phenomena or the properties that we can observe 
. . . then if the inferences are confirmed by subsequent experiment, the 
hypothesis will acquire a degree of probability approximating to what in 
physics is called certainty. 

With arguments such as this Avogadro and Ampere sapped the 
foundation i.e., the pile-of-shot model of a gas of arguments (3) 


and (4) against the "equal volumes-equal numbers" idea. Also, regard- 
ing the controversy from the outside, Avogadro was, unlike Dalton, 
prepared to accept Gay-Lussac's conclusion at its face value, so that 
argument (5) - to the effect that Gay-Lussac's law represents only a 
crude approximation to reality failed to impress him. Consequently, 
in the sequel, Avogadro had only to dispose of points (i) and (2) 
which, as already remarked, represent much more difficult considera- 

The special cases discussed by Avogadro in the continuation of his 
discourse are most readily construed in terms of a general formulation 
of his argument. If the density of gas A is taken as d A9 and that of 
gas B as d B , then d A and d B represent the weights of unit volumes of 
the two gases, measured under the same conditions of temperature and 
pressure. By Avogadro's hypothesis, the numbers of gas particles 
present in each case are identical. Calling this number n, it is plain that 

n X Particle weight of A __ d A 
n X Particle weight of B d B * 


Particle weight of A _ d A 
Particle weight of B d^' 

Here we have an expression from which the relative particle weights 
can be calculated from the measured gas densities. This calculation is 
most conveniently carried out if the particle weight of one gas is defined 
as a standard e.g., the weight of the hydrogen particle may be taken 
as unity after which numerical values can be assigned to the particle 
weights of all the other gases, on the basis of the relative gas densities. 
Thus, oxygen gas being (according to Avogadro's evaluation) fifteen 
times as dense as hydrogen, the weight of the gaseous particle of 
oxygen is 15 relative to the hydrogen particle taken as i. 

With regard to the numbers of particles combining in a given re- 
action, if V A unit volumes of gas A react with V B unit volumes of 
gas B, then if n is taken as defined above, we must have nV A particles 
of A reacting with nV s particles of B. Consequently, for the relative 
numbers of particles entering into the reaction we have 

Number of particles of A _ nV A __ V A 
Number of particles of B nV B V s 

so that from the ratio of the combining volumes we may deduce the 
relative numbers of particles involved in the reaction. Thus, since two 
volumes of hydrogen react with one volume of oxygen to give water, 

282 CASE 4 

there are two particles of hydrogen for every particle of oxygen involved 
in this reaction. 

It should be noted that both of these important calculations were 
possible only because of Avogadro's basic simplifying assumption, that 
equal volumes of different gases contain the same number of particles, 

Let us now return to Avogadro's text. 

Setting out from this hypothesis [i.e., the "equal volumes-equal num- 
bers" idea] it is apparent that we have the means of determining very 
easily the relative masses of the molecules of substances obtainable in 
the gaseous state, and the relative number of these molecules in com- 
pounds; for the ratios of the masses of the molecules are then the same as 
those of the densities of the different gases at equal temperature and 
pressure, and the relative number of molecules in a compound is given at 
once by the ratio of the volumes of the gases that form it. For example, 
since the numbers 1.10359 and 0.07321 express the densities [i.e., specific 
gravities] of the two gases oxygen and hydrogen compared to that of 
atmospheric air as unity, and the ratio of the two numbers consequently 
represents the ratio between the masses of equal volumes of these two 
gases, it will also represent on our hypothesis the ratio of the masses of 
their molecules. Thus the mass of the molecule of oxygen will be about 
15 times that of the molecule of hydrogen, or, more exactly, as 15.074 to i. 
In the same way the mass of the molecule of nitrogen will be to that of 
hydrogen as 0.96913 to 0.07321, that is, as 13, or more exactly 13.238, to i. 
On the other hand, since we know that the ratio of the volumes of 
hydrogen and oxygen in the formation of water is 2 to i, it follows that 
water results from the union of each molecule of oxygen with two 
molecules of hydrogen. Similarly, according to the proportions by volume 
established by M. Gay-Lussac for the elements of ammonia, nitrous oxide, 
nitrous gas and nitric acid, ammonia will result from the union of one 
molecule of nitrogen with three of hydrogen, nitrous oxide from one 
molecule of oxygen with two of nitrogen, nitrous gas from one molecule 
of nitrogen with one of oxygen, and nitric acid from one of nitrogen with 
two of oxygen. 


There is a consideration that appears at first sight to be opposed to the 
admission of our hypothesis with respect to compound substances. It 
seems that a molecule composed of two or more elementary molecules 
should have its mass equal to the sum of the masses of these molecules; 
and that in particular, if in a compound one molecule of one substance 
unites with two or more molecules of another substance, the number of 
compound molecules should remain the same as the number of molecules 
of the first substance. Accordingly, on our hypothesis, when a gas com- 
bines with two or more times its volume of another gas, the resulting 


compound, if gaseous, must have a volume equal to that of the first of 

these gases. 

Consider the case in which unit volume of gas A reacts with V s 
volumes of gas B, where V B is greater than unity. Letting n represent 
the number of particles in unit volume of any gas, it is apparent that 
we then have n particles of A reacting with nV B particles of B. If each 
molecule of the product contains one particle (atom) of A then, plainly, 
we cannot have more than n molecules of product; and, consequently, 
we would expect to find no more than unit volume of this product. 

Avogadro continues: 

Now, in general, this does not in fact occur. For instance, the volume 
of water in the gaseous state is, as M. Gay-Lussac has shown, double that 
of the oxygen which enters into it, or, what comes to the same thing, 
equal to that of the hydrogen instead of being equal to that of the 
oxygen. But a means of explaining facts of this type in conformity with 
our hypothesis presents itself naturally enough. We suppose that the 
constituent molecules of any simple gas (i,e., the molecules that are at 
such a distance from each other that they cannot exert their mutual 
action) are not formed of only one elementary molecule [atom], but are 
made up of a certain number of these molecules united by attraction to 
form a single whole. Further, that when such molecules unite with 
those of another substance to form a compound molecule, the integral 
molecule which should result splits up into two or more parts (or integral 
molecules), each composed of half, quarter, &c., the number of elemen- 
tary molecules forming the constituent molecule of the first substance, 
combined with half, quarter, &c., the number of constituent molecules of 
the second substance that ought to enter into combination with one 
constituent molecule of the first substance. . . . This is supposed to 
occur in such a way that the number of integral molecules of the com- 
pound becomes double, quadruple, &c., what it would have been if there 
had been no splitting up, and exactly what is necessary to satisfy the 
volume of the resulting gas. Thus, for example, the integral molecule of 
water will be composed of a half-molecule of oxygen with one molecule, 
or, what is the same thing, two half-molecules of hydrogen. 

Here we have the heart of Avogadro's second major and, apparently, 
entirely original, contribution : the idea of polyatomic molecules of the 
gaseous elements. 

Avogadro had previously convinced himself that, if equal volumes 
of different gases contained equal numbers of the respective particles, 
then, whenever unequal volumes of different elementary gases took 
part in some chemical combination, the volume of any gaseous reaction 
product should not exceed the volume of that one of the reacting gases 
which was involved in smaller quantity. However, this prediction was 

284 CASE 4 

flatly contradicted by well-known experimental facts. For example, 
Gay-Lussac and von Humboldt had shown (see page 251) that when 
one volume of oxygen combined with two volumes of hydrogen, two 
volumes of water vapor were formed. Now if these volume relations 
are construed in terms of Avogadro's first assumption that there is 
always the same number (n) of particles in unit volumes of different 
gases they suggest that n particles of oxygen react with 2n particles 
of hydrogen to give 2n particles of water vapor. As already mentioned, 
this might imply that in some way each of the oxygen particles is 
divided into two fragments, one of which is incorporated in each of 
the water molecules. 

Viewed on the basis of the implicit assumption that the "particles" 
of gaseous oxygen are identical with oxygen atoms, the suggested sub- 
division (of atoms), opposed as it was to the fundamental tenet of the 
atomic theory, was not entertained as a serious possibility. And indeed, 
the postulated indivisibility of the chemical atom was strongly but- 
tressed by the very existence of the laws of definite, multiple, and 
equivalent proportions, which were so well explained in terms of the 
atomic theory. But Avogadro was sufficiently acute to perceive that, 
despite the superficial plausibility of the identification of the "particles" 
of the gaseous elements with the chemical atoms of those elements, 
this identification was in fact an arbitrary one, unsupported by any 
experimental evidence. To be sure, this was the simplest possibility, 
but Avogadro came to regard it as an oversimplification. He suggested, 
instead, that the "particles" present in the gaseous elements do not 
consist of the individual atoms of the elements but of groups of atoms 
of the same element joined in a single molecule of that element. That 
is, the particles that, in the gaseous elements, behave as essentially in- 
dependent entities (i.e., "the molecules that are at such a distance from 
each other that they cannot exercise their mutual action") are not, as 
had been generally believed, single atoms, but consist of two or more 
atoms of the same element. 

Now if we were to suppose that the oxygen "particle" contained, 
say, two oxygen atoms, it would then be possible to divide it into two 
equal fragments (atoms) without in any way threatening the integrity 
of the individual oxygen atoms. Thus from the n oxygen "particles" 
(O 2 molecules each containing two oxygen atoms) in one volume of 
oxygen we could obtain 2# oxygen atoms, sufficient to form the 2# 
molecules of water vapor required to fill two volumes of this gas. If we 
further assume that the "particle" of gaseous hydrogen is a molecule 
similarly constituted of two atoms (i.e., H 2 ), we can then formulate 
the reaction of oxygen with hydrogen, to give water, in the following 


i volume oxygen + 2 volumes hydrogen 2 volumes water vapor, 

n particles + 2n particles - 2n particles, 

n O 2 + 2n H 2 - [H 4 O 2 ] - 2* H 2 O; 

or, most simply, 

O 2 + 2 H 2 -> [H 4 O 2 ] -> 2 H 2 O. 

The bracketed term [H 4 O 2 ] in the chemical equation represents the 
"integral molecule" which Avogadro imagined was first formed by the 
combination of one particle of oxygen with two of hydrogen. This 
"integral molecule" was then supposed to "split up" spontaneously, 
to form two H 2 O molecules as a final product. This transient inter- 
mediate was entirely conjectural, since Avogadro had no knowledge 
save of the initial reactants and the final products. And, indeed, the 
reaction actually proceeds through a much more complicated "mech- 
anism" which is still only imperfectly understood. Current practice is 
to omit from the chemical equation all such unstable intermediate 
compounds, showing only the initial reactants and the final products. 
However, the intermediates to which Avogadro refers will be shown 
here, in brackets as above. 

It will be seen that in the foregoing case Avogadro, with the aid of 
his ingenious second assumption, namely, the existence of polyatomic 
molecules of elements, has succeeded in reconciling the "equal vol- 
umes-equal numbers" idea suggested by Gay-Lussac's law of combin- 
ing volumes with the indivisibility of the chemical atom so strongly 
championed by Dalton. Now the apparent difficulty in achieving such 
a reconciliation was one of the points stressed by Dalton in his attack 
on the validity of Gay-Lussac's law. But all the troublesome instances 
comprehended under this argument (a few are listed on page 276) 
can now be dealt with satisfactorily, as is illustrated in the following 
examples. Note that in every case the number of molecules of each gas 
is directly proportional to the volume of that gas, and, further, that 
this harmonization with the "equal volumes-equal numbers" idea can 
now be secured without "splitting" any atoms, but by merely sub- 
dividing polyatomic molecules. 

i volume oxygen + solid carbon 2 volumes carbon monoxide, 
n particles -> 2/2 particles, 

O 2 + 2 C ~ 2 CO. 

T volume nitrogen + i volume oxygen > 2 volumes nitrous gas, 
n particles + n particles - 2n particles, 
N 2 + 2 - [N 2 2 ] - 2 NO. 

286 CASE 4 

3 volumes hydrogen + i volume nitrogen ~ 2 volumes ammonia, 
yi particles + n particles in particles, 
3 H 2 + N 2 -> [N 2 H 6 ] - 2 NH 3 , 

The last two cases are mentioned by Avogadro in the next paragraph 
of his text, where he also cites the following reaction: 

2 volumes nitrogen + i volume oxygen 2 volumes nitrous oxide, 

("laughing gas") 

2n particles + n particles - 2n particles, 

2 N 2 + O 2 - [N 4 O 2 ] - 2 N 2 O. 

Thus argument (i) (see page 276) against the "equal volumes equal 
numbers" idea can be neatly side-stepped by postulating the existence 
of polyatomic molecules of the gaseous elements. It will be recalled 
that arguments (3), (4), and (5) were dismissed previously (see page 
75), so we have only to deal with argument (2), which called atten- 
tion to certain apparent anomalies in the measured gaseous densities. 
Avogadro does not discuss this point explicitly, but it is easy to see 
how these difficulties can be dissipated with the aid of formulations 
such as those that have been given above. 

Among the anomalies of this type we may remark: steam, formed 
from oxygen plus hydrogen, is less dense thiui oxygen itself; carbon 
monoxide, formed from oxygen plus carbon, is less dense than oxygen; 
and ammonia, formed from nitrogen plus hydrogen, is less dense than 
nitrogen. It at first appears that the product molecules formed by such 
addition reactions must be heavier than the particles of the starting 
material; so that, if unit volume of each of these gases contains the 
same number of particles, water vapor and carbon monoxide should 
both be more dense than oxygen, and ammonia more dense than 
nitrogen, contrary to the experimental findings. But Avogadro's new 
formulation clearly indicates how these contradictions can be obviated. 
What had been assumed to be addition reactions were now seen to 
be, in effect, substitution reactions. Thus in the formation of the mole- 
cules of water vapor (H 2 O) two hydrogen atoms have been substi- 
tuted for one of the oxygen atoms in the oxygen molecule (O 2 ). Since 
two hydrogen atoms together weigh less than one oxygen atom, the 
water molecule should be lighter than the oxygen molecule. Thus if 
the weights of unit volumes of these gases are compared it is now 
only to be expected that the water vapor will prove less dense than 
the oxygen, as is indeed the case. In the same way, carbon monoxide 
is formed by the substitution of a carbon atom for a heavier oxygen 
atom in the oxygen molecule, so that the carbon monoxide molecule 


should weigh less than one of oxygen. Similarly, the substitution of 
three hydrogen atoms for one of the nitrogen atoms in the nitrogen 
molecule (N 2 ) yields a molecule of ammonia (NH 3 ) weighing less 

than the "nitrogen molecule itself. In this way the last of the major 
arguments advanced against the "equal volumes-equal numbers" idea 
can be disposed of, and it is plain that Avogadro's double hypothesis 
provides answers to all the difficulties to which Dalton called attention. 
Avogadro's exposition of the important applications of his double 
hypothesis, continues. 

On reviewing the various compound gases most generally known, I 
only find examples of duplication of the volume relatively to the volume 
of that one of the constituents which combines with one or more volumes 
of the other; we have already seen this for water. In the same way, we 
know that the volume of ammonia gas is twice that of the nitrogen 
which enters into it. M. Gay-Lussac has also shown that the volume of 
nitrous oxide is equal to that of the nitrogen which forms part of it, and 
consequently is twice that of the oxygen. Finally, nitrous gas, which 
contains equal volumes of nitrogen and oxygen, has a volume equal to 
the sum of those of the two component gases, that is to say, double that 
of each of them. Thus in all these cases there must be a division of the 
molecule into two; but it is possible that in other cases the division might 
be into four, eight, &c. The possibility of this division of compound 
molecules might have been conjectured a priori '; for otherwise the integral 
molecules of bodies composed of several substances with a relatively large 
number of molecules, would come to have a mass excessive in comparison 
with the molecules of simple substances. We might therefore imagine 
that nature had some means of bringing them back to the range of the 
latter, and the facts have indicated the existence of such means. Besides, 
there is another consideration that would seem to make us admit in some 
cases the division in question; for how could one otherwise conceive a 
real combination between two gaseous substances uniting in equal vol- 
umes without condensation, such as takes place in the formation of 
nitrous gas? Supposing the molecules to remain at such a distance that 
the mutual attraction of those of each gas could not be exercised, we 
cannot suppose that a new attraction could take place between the mole- 
cules of one gas and those of the other. But on the hypothesis of division 
of the molecule, it is easy to see that the combination really reduces two 
different molecules to one, and that there would be contraction by the 
whole volume of one of the gases if each compound molecule did not 
split up into two molecules of the same nature. M, Gay-Lussac saw 
clearly that according to the facts the diminution of volume in the com- 
bination of gases could not represent the closer approach of their mole- 
cules. The splitting of the molecules in such combinations explains how 
these two things can be rendered independent of one another. 

288 CASE 4 

Avogadro suggests that It is very difficult to construe the reaction 
i volume nitrogen + i volume oxygen 2 volumes nitrous gas 

except in terms of his double hypothesis. For the first stage of this 
reaction he proposes 

N 2 + 2 - [N 2 2 ], 

where the N 2 O 2 is to be regarded as an unstable intermediate, since 
"there would be contraction by the whole volume of one of the gases 
if each compound molecule did not split up into two molecules of the 
same nature." Therefore the over-all reaction has the form 

N 2 + 2 -> [N 2 2 ] ~* 2 NO, 
n particles + n particles > in particles. 

This is entirely compatible with the observed fact that the reaction 
proceeds without apparent volume contraction, since the total numbers 
of particles present before and after the reaction are identical, even 
though a real combination has taken place. 


Dalton, on arbitrary suppositions that appeared to him most natural 
[i.e., the rule of greatest simplicity] as to the relative number of mole- 
cules in compounds, has endeavored to establish ratios between the 
masses of the molecules of simple substances. Our hypothesis, supposing 
it well-founded, puts us in a position to confirm or rectify his results 
from precise data, and, above all, to assign the size of compound mole- 
cules according to the volumes of the gaseous compounds, which de- 
pends partly on that division of molecules of which this physicist had no 

Avogadro emphasizes that all of Dalton's atomic weights ultimately 
depend on the assignments of molecular formulas made with the aid 
of the not implausible, but entirely unsupported, "rule of greatest 
simplicity." Avogadro suggests that a superior method for the evalua- 
tion of these molecular formulas and atomic weights can be founded 
on his own double hypothesis. We have already remarked (see page 250) 
that the chief obstacle to the further extension and application of 
Dalton's atomic theory lay in that theory's inability to place its molecu- 
lar formulas (and, thence, its atomic weights) on a rational empirical 
basis. Consequently, Avogadro's present proposal should be regarded 
as a crucial step in the development of the atomic theory. 

In what follows I shall make use of the exposition of Dalton's ideas 
that Thompson has given us in his System of Chemistry. Dalton sup- 


poses that water is formed by the union of hydrogen and oxygen, mole- 
cule to molecule. From this it results, according to the ratio by weight 
of the two components, that the mass of the molecule of oxygen should 
be to that of hydrogen about as 7% to i or, according to Dalton's evalua- 
tion, as 6 to i. This ratio on our hypothesis is, as we have seen, twice as 
great, namely, as 15 to i. As for the molecule of water, its mass ought to 
be roughly expressed by 15 + 2 = 17 (taking for unity that of hydro- 
gen), if there were no division of the molecule into two; but on account 
of this division it is reduced to half, 8%, or more exactly 8.537, as may 
also be found directly by dividing the density of aqueous vapour, 0.625 
according to Gay-Lussac, by the density of hydrogen, 0.0732. This mass 
only differs from 7, that assigned to it by Dalton, by the difference in the 
values for the composition of water; so that in this respect Dalton's result 
is approximately correct from the combination of two compensating 
errors that in the mass of the molecule of oxygen, and that of neglect- 
ing the division of the molecule. 

Caution must be exercised in making any comparison of Avogadro's 
results with those o Dalton. To begin with, the two sets of calcula- 
tions were based on somewhat different analytical data. More important, 
we have now reached the very point at which Avogadro's suggestion 
of a distinction between the physically "smallest particle" (i.e., the 
molecule of an element) and the chemically "smallest particle'* (i.e., 
the atom of an element) leads to a reorganization of the atomic-weight 
scale proposed by Dalton. 

Observing that the experimental data indicated the density of oxygen 
to be 15 times that of hydrogen, Avogadro deduced, with the aid of his 
"equal volumes-equal numbers" hypothesis, that the molecular weight 
of oxygen was 15, relative to the hydrogen molecule taken as i. He 
then made use of Gay-Lussac's data on combining volumes 2 volumes 
o hydrogen react with i of oxygen to give 2 of water vapor as the 
basis for the following formulation of the reaction in which water 
is so produced 

2 H 2 + O 2 -> [H 4 O 2 ] - 2 H 2 O 

The spontaneously unstable aggregate H 4 O 2 is composed of two 
hydrogen molecules (each, by definition, of weight i) and one oxygen 
molecule (whose relative atomic weight has been calculated as 15). 
Therefore the unstable aggregate must have a relative weight of 17; 
and when it splits in half to form two water molecules (H 2 O) each 
of these will have a molecular weight o 854, relative to the hydrogen 
molecule taken as i. This value is confirmed by the fact that water 
vapor is 8 l / 2 times as dense as hydrogen gas. 

Compare this with Dalton's procedure. Taking the formula of 
water as HO, Dalton used his combining weights 6 of oxygen com- 



bine with i of hydrogen to give 7 of water to calculate the relative 
atomic weight of oxygen as 6. This evaluation leads to a molecular 
weight of water of 7 (i.e., 6 + i), relative to the hydrogen atom taken 
as i. Numerically, this value, 7, differs from that deduced by Avogadro, 
SVz, only "by the difference in the values for the composition of water" 
Thus, had Dalton employed the more accurate combining weights 
cited by Avogadro (7% of oxygen combining with i of hydrogen to 
give 8*/2 of water) his value for the atomic weight of oxygen would 
have been 7 1 /z, and for the molecular weight of water, 8%. 

However, despite this agreement of the numerical values assigned 
to the molecular weight of water, Avogadro very properly remarks 
that Dalton obtained the "correct" figure only through "the combina- 
tion of two compensating errors that in the mass of the molecule 
of oxygen, and that of neglecting the division of the molecule." The 
way in which these errors cancel in the present case can best be illus- 
trated by the following diagram: 



Dalton's combining weights 

More accurate combining 
weights, available in 1811 

2 water 

Avogadro: <$> + <[> + 



All these numbers refer to the hydrogen "particle" (Dalton 
Avogadro <J> ) taken as i. 

Avogadro now continues with his consideration of a variety of spe- 
cific applications of his new methods for the evaluation of molecular for- 
mulas and molecular weights. He carefully shows how his own values 
are derived, with the aid of his double hypothesis, from combining 
volume and density data for gases, while Dalton's figures are seen to 
derive from combining weight data, interpreted with the aid of the 
"rule of greatest simplicity." 

Dalton supposes that in nitrous gas the combination of nitrogen and 
oxygen takes place molecule to molecule: we have seen that this is 
effectively so on our hypothesis. Thus Dalton would have found the 
same molecular mass for nitrogen as we have, always supposing that of 
hydrogen to be unity, if he had not set out from a different evaluation 
of that of oxygen, and if he had taken precisely the same evaluation of 


the quantities of the elements in nitrous gas by weight. But in supposing 
the molecule of oxygen to be less than half what we find, he had also 
to make that of nitrogen equal to less than half the value we have 
assigned to it, viz., 5 instead of 13. As for the molecule of nitrous gas 
itself, his neglect of the division of the molecule again makes his result 
approach ours; he has made it 6 + 5 = n, whilst according to us it is 

, - - , 

j^ or more exactly - = 14.156, as we 

also find by dividing 1.03636, the density of nitrous gas according to 
Gay-Lussac, by 0.07321 [the density of hydrogen]. Dalton has also de- 
termined in the same manner as the facts have given it to us, the relative 
number of molecules in nitrous oxide and in nitric acid, and in the first 
case the same circumstance has rectified his result for the magnitude of 
the molecule. He makes it 6 + 2X5= *6> whilst according to our 

15.074 -f- 2 X - 

method it should be - = 20.775, a number which is 


also obtained by dividing 1.52092, the density of nitrous oxide gas ac- 
cording to Gay-Lussac, by the density of hydrogen gas. 

As for ammonia, Dalton's supposition as to the relative number of 
molecules in its composition is on our hypothesis entirely at fault. He 
supposes nitrogen and hydrogen to be united in it molecule to molecule, 
whereas we have seen that one molecule of nitrogen is in it joined with 
three molecules of hydrogen. According to him the molecule of ammonia 

would be 5 + i = 6; according to us it should be - = 8, or more 


exactly 8.119, as may also be deduced directly from the density of am- 
monia gas. The division of the molecule, which does not enter into 
Dalton's calculations, here again corrects in part the error that would 
result from his other suppositions . . . 

Avogadro goes on to extend his new mode of calculation to a wide 
variety of other concrete cases. Up to this point practically all his 
statements and deductions are essentially correct, but in his further 
discourse he rather overextends himself, in venturing out over more 
slippery ground. Some of his later conclusions are not entirely free 
from error, though they still constitute an impressive demonstration 
of the power of his new technique for the evaluation of the molecular 
formulas and molecular weights so essential to the further progress 
of the atomic theory. In his concluding paragraph Avogadro very 
appropriately indicates the satisfaction of this need as one of the chief 
fruits of his investigation. In this closing statement Avogadro also 

292 CASE 4 

bears testimony to the profound contemporary impression made by 
Berthollet's conception of compound formation in /^definite propor- 
tions. Just as did Gay-Lussac under similar circumstances (see page 
262) Avogadro attempts to supply some reconciliation of Dalton's new 
conceptual scheme of which he so obviously approves with the 
older views of Berthollet that he is still reluctant to abandon entirely. 

It will have been in general remarked on reading this Memoir that 
there are many points of agreement between our special results and those 
of Dalton, although we set out from a general principle, and Dalton has 
only been guided by considerations of detail. This agreement is an argu- 
ment in favour of our hypothesis, which is at bottom merely Dalton's 
system furnished with a new means of precision through the connection 
we have found between it and the general fact established by M. Gay- 
Lussac. Dalton's system supposes that compounds are made in general in 
fixed proportions, and this is what experiment shows with regard to the 
more stable compounds and those most interesting to the chemist. It 
would appear that it is only combinations of this sort that can take place 
amongst gases, on account of the enormous size of the molecules that 
would result from ratios expressed by larger numbers, in spite of the 
division of the molecules, which is in all probability confined within 
narrow limits. We perceive that the close packing of the molecules in 
solids and liquids, which only leaves between the integral molecules 
distances of the same order as those between the elementary molecules, 
can give rise to more complicated ratios, and even to combinations in all 
proportions; but these compounds will be so to speak of a different type 
from those with which we have been concerned, and this distinction may 
serve to reconcile M. Berthollet's ideas as to compounds with the theory 
of fixed proportions. 


Avogadro's proposals were essentially sound, yet in the years 
between 1811 and 1858 they were almost completely ignored by the 
vast majority of chemists. Instead, a number of other methods were 
employed in various attempts to establish molecular formulas and 
atomic weights. By 1840 the variety and fallibility of these methods 
had led to a number of basically contradictory results. The resulting 
confusion engendered an increasingly strong feeling that atomic 
weights could never be unambiguously determined, and that the 
whole atomic theory might be no more than a speculation that had 
outworn its usefulness as a quantitative concept, though everyone rec- 
ognized its ancient value as a way of thinking about natural phe- 


In 1858 Cannizzaro revived and slightly, but very importantly, ex- 
tended Avogadro's ideas. His formulation rapidly won widespread ac- 
ceptance for Avogadro's original proposals and the position of the 
atomic-molecular theory has since then steadily become more secure. 
Although we cannot consider them, in detail it may be of interest to 
examine some of the factors that contributed to, and some of the 
salient events in, this long period of uncertainty. 

Some Persisting Objections to Avogadro's Proposals. Avogadro's 
contribution was a very real one. It led to a reasonable method for the 
derivation of molecular formulas the very information of which 
Dalton's atomic theory stood most in need. But its importance could 
not disguise the shortcomings of Avogadro's work. We have already 
mentioned that his presentation was anything but lucid. More impor- 
tant, the applicability of Avogadro's proposal was severely limited. It 
could be applied only to elements and compounds that could be readily 
obtained in a gaseous condition, and unfortunately the vast majority of 
materials do not exist as gases under normal conditions of temperature 
and pressure. Very possibly Avogadro recognized this shortcoming, 
for in the latter part of his first paper, and in his subsequent papers, 
he attempted to extend his methods to the determination of the for- 
mulas of solid substances. However, such a gross overextension of 
methods that rather clearly applied only to gases and vapors simply 
weakened the effect of those arguments in which Avogadro was quite 

While such factors may have reduced the initial impact of Avo- 
gadro's work, there were other more fundamental objections to his 
proposal. It should be recalled that this proposal rested on two assump- 
tions. The first of these, the "equal volumes-equal numbers" idea, 
was not intrinsically unlikely, though it was distinctly ad hoc and un- 
supported. The second closely related assumption was that, even as 
stable groupings of atoms of different fynds were capable of coordinated 
existence and action in the molecule of a compound, there could also 
be a stable grouping of atoms of the same tynd, to form a molecule 
of an element. Let us now examine three of the graver difficulties 
that beset this postulation of polyatomic molecules of the elements, at 
the time it was proposed by Avogadro. 

(i) Although there was no evidence definitely against this ad hoc 
assumption, neither was there much evidence for it. To be sure, it rec- 
onciled Avogadro's first assumption with the known volume relations 
and the indivisibility of the chemical atom. But Avogadro's first as- 
sumption was very tenuously supported, so that his second assumption 
must have appeared to represent the piling on of one unsupported 
speculation in an attempt to maintain another conjectural notion. 

294 CASE 4 

Furthermore, there is some irrationality in the suggestion that the 
physically "smallest particle" (molecule) of a gas is not the "smallest 
particle" the chemical atom but rather an aggregate of such atoms. 

(2) The suggestion that there were definite molecules of elements, 
containing two, four, six, or more atoms of the same kind, raised 
certain problems. If gaseous "atoms" can so combine, it means that 
there must be some attractive forces between atoms of the same kind. 
Speculation about such attractive forces seemed utterly ridiculous to 
Dalton, among others, and three years before Avogadro's paper ap- 
peared we find him animadverting on this point. In connection with 
a criticism of some work of Berthollet's he says in his New System : 

The author means to say, that the parts of elastic fluids are endued 
with the force of cohesion; but this he applies only to heterogeneous 
[different kinds of] particles. He certainly does not mean that particles 
of homogeneous elastic fluids possess the force of cohesion. [Note the 
complete confidence with which this "absurd" possibility is rejected.] 

Newton has demonstrated from the phenomena of condensation and 
rarefaction that elastic fluids are constituted of particles, which repel one 
another by forces which increase in proportion as the distance of their 
centres diminishes: in other words, the forces are reciprocally as the 
distances. This deduction will stand as long as the Laws of elastic fluids 
continue to be what they are. What a pity it is that all who attempt to 
reason, or to theorize respecting the constitution of elastic fluids, should 
not make themselves thoroughly acquainted with this immutable Law, 
and constantly hold it in their view whenever they start any new project. 

Although Newton's "Law" was not so "immutable" as Dalton be- 
lieved (see page 223) it was difficult to imagine how gaseous particles 
might sometimes repel each other to produce the "spring of the air" 
expressed in Boyle's law, yet on other occasions attract each other to 
form groups of atoms of the same kind. 

Even allowing that some attractive forces might exist, why should 
they stop with the formation of O 2 , rather than continuing in action 
to form O 3 , O 4 , and so on? That is, why should one atom of oxygen 
attract another atom of oxygen, to form O 2 , while one O 2 particle 
repels another O 2 particle (producing the behavior expressed in Boyle's 
law) rather than combining with it to form O 4 ? No satisfactory answer 
to these last questions could be given by Avogadro and, indeed, no 
"good" answer could be given until about 1925. It is little wonder, 
then, that Avogadro's proposition provoked a skeptical response from 
his contemporaries. 

(3) Avogadro himself recognizes that it is possible that larger 
numbers of atoms of the same kind may be combined in a single 
gaseous particle. Thus it is quite possible that instead of O 2 molecules 


we have O 4 molecules. Instead of writing, as we did in the last section, 

2 H 2 + O 2 - 2 H 2 O, 
perhaps we should have written 

2 H 2 + O 4 - H 2 O 2 . 

The then available data did not allow of a decision between these al- 
ternatives, and it was almost 50 years before Avogadro's countryman, 
Cannizzaro, suggested a simple way of securing a highly probable 
(though not "certain") experimental distinction. 

These are formidable difficulties. The first the highly speculative 
character of the double assumption was an entirely unavoidable, but 
none the less serious, shortcoming. However, the second and third 
difficulties the unexplained stability of the polyatomic molecules of 
the elements, and the indeterminacy of the number of atoms that 
they contained were, then and later, even more serious obstacles. 
Had Avogadro's proposal been the only obvious way of reconciling 
the atomic theory and the law of combining volumes perhaps these 
difficulties could have been taken in stride. However, as we shall see, 
there was at hand an alternative explanation of the data which, at 
the time, presented a much more prepossessing appearance. 

The second difficulty the unexplained stability of the polyatomic 
molecules of the elements was, in 1811, a particularly annoying one. 
The postulation of such molecules appeared to be a flagrant contra- 
diction of the most alluring explanation that could then be given of 
the striking chemical effects brought about by electricity. These effects 
and this explanation were very much in the minds of contemporary 
investigators, since they had developed very recently. A brief examina- 
tion of some of the more important aspects of this work may now 
be appropriate. 

The Electrochemical Investigations of Davy and Berzelius, and the 
Development of the Dualistic Theory. The vigorous activity in the 
field of electrochemical investigations largely stemmed from the in- 
vention of the voltaic pile. This pile was, in effect, a primitive battery 
not essentially different from batteries that are used today. It produced 
much stronger electric currents than had previously been available, 
and the application of this new tool to the study of chemical pheno- 
mena was undertaken with great celerity and astonishing results. 

Volta's description of his pile was communicated early in 1800 in 
the form of a letter to Sir Joseph Banks, then president of the Royal 
Society. Within a few months two English investigators had found 
that the establishment of an electric current in water led to the de- 
composition of this substance and the formation of hydrogen and 

296 CASE 4 

oxygen in roughly the proportions in which they normally combined 
to form water. Apparently the electric current had resolved the com- 
pound into its component elements. Similar decompositions o other 
compounds were rapidly discovered, notably in an important series o 
observations reported in 1803 by Berzelius and Hisinger. But the most 
important discoveries on the "Chemical Agencies of Electricity" were 
made through prolonged and systematic studies carried on with great 
virtuosity and notable eclat by Sir Humphry Davy, working at the 
Royal Institution. 6 

Davy's further work resulted, in 1807, in his spectacular discovery 
of the alkali metals, to which he was guided by a belief that the 
stability of chemical compounds was due to electrical forces between 
the elementary particles (i.e., atoms) of which they were composed. 
Davy's remarks in this connection retain a remarkable cogency even 

If chemical union be of the [electrical] nature which I have ventured 
to suppose, however strong the natural electrical energies of the elements 
of bodies may be, yet there is every probability of a limit to their 
strength; whereas the powers of our artificial instruments seem capable 
of indefinite increase . . . [Consequently, we may] hope that the new 
[electrical] method of analysis may lead us to the discovery of the true 
elements of bodies. 7 

Using a much enlarged voltaic pile, Davy succeeded in breaking 
down several previously undecomposed substances, and found among 
their components the alkali elements "true" chemical elements 
whose existence Lavoisier had formerly been able at most to suspect. 
In this connection we may note a remark of Dalton's that has already 
been cited (see page 228) : "We may not know what elements are 
absolutely indecomposable, and what are refractory, because we do 

8 Indeed, in 1806 a paper on this subject won for Davy a prize offered by Napoleon 
for the most important electrical work of the year. Coming shortly after the Battle of 
Trafalgar and in the same year as the "Continental System" of blockading England, this 
award may occasion rather melancholy reflections today. To the cultural historian remains 
the interesting task of explaining how, in the development of Western civilization, the 
growth of science, from a harmless and relatively useless avocation of a few amateurs, to 
its present eminence as a major contributor to national welfare, entailed the loss of its 
once-vaunted supranational character. 

7 There is an almost perfect parallelism between these views of Davy's and opinions 
that are entertained today. Believing as we do that electrical forces are responsible not 
only for the existence of chemical compounds, but also for the existence of the chemical 
"elements" themselves and the various "particles" of which these "elements" are now 
presumed to be composed, we are still seeking, as by the construction of bigger and better 
cyclotrons, to achieve an "indefinite increase" in the power of our instruments. We hope 
that with such instruments it will be possible to resolve the "elements" that we already 
know into yet more subtle "materials," to find the "true elements*' of which, we now 
believe, the chemical "elements" are themselves compounded. 


not apply the proper means for their reduction." Davy had discovered 
the "proper means" to apply to some of these "refractory" materials. 

Davy's demonstration of the ability of electrical influences to work 
a separation of even the most resistant chemical compounds was very 
impressive. Duly considered, it lent force to the idea that chemical 
compounds owed their stability to the electric forces between the atoms 
of which they were composed. In Davy's experiments, these forces were 
simply overcome by the more powerful disruptive forces generated by 
the enlarged voltaic pile. This electrochemical theory of chemical com- 
bination received its most elaborate formulation and most vigorous 
expression in the dualistic theory of the Swedish chemist Berzelius. 
In this theory Berzelius made the new findings on electrochemical 
phenomena the basis of a revision and revival of another (acid-base) 
dualistic system that had been suggested by Lavoisier, who had in 
turn derived his dualistic views from even more ancient natural 

The decomposition of compounds by an electric current (called 
electrolysis} was brought about by inserting in the substance, or in a 
solution of it, two terminals (called electrodes) that were, in turn, 
connected to the voltaic pile. The products of the decomposition then 
appeared at the electrodes. Thus, in the electrolysis of water, it was 
found that at one electrode only hydrogen was liberated, and at the 
other only oxygen. This behavior, when considered in the light of 
what was already known about the forces acting between charged 
bodies, naturally suggested that all the hydrogen particles bore one 
characteristic charge, while all the oxygen particles carried an equally 
characteristic charge of opposite polarity. In the attractive forces known 
to exist between such oppositely charged particles Berzelius saw the 
origin of the stability of the chemical compound, water. Furthermore, 
his work on the electrolysis of a number of other compounds showed 
that some of the decomposition products always appeared at one 
electrode, and the others at the oppositely charged electrode. This 
seemed to be a fairly clear indication that the different constituents 
of all compounds were always oppositely charged, and suggested that 
all chemical compounds owed their stability to the electric forces be- 
tween the oppositely charged particles of which they were composed. 
This was the heart of Berzelius' dualistic theory the dualism in- 
hering in the juxtaposition of positively and negatively charged bodies. 
In this theory electrolysis was construed as a simple reversal of normal 
chemical combination. That is, the charges characteristic of the free 
elements, which had been lost or neutralized in their combination, were 
restored at the appropriate electrodes; and, thereby, the compound was 
broken down and the free elements were regenerated. 

298 CASE 4 

An early intimation of Berzelius' dualistic theory appeared in the 
same year, indeed in the same journal, in which Avogadro's proposal 
was published. However, it is easy to see how Berzelius, and the many 
who acceded to the dualistic conceptions of this preeminent theore- 
tician, would be inclined to take a very dim view of Avogadro's pos- 
tulation of polyatomic molecules of the elements. They readily "un- 
derstood" the stability of water in terms of the aggregation of the 
oppositely charged particles that composed it. But how could one, 
with this dualistic conception, imagine the stable existence of the 
hydrogen molecules and oxygen molecules hypothesized by Avogadro? 
Electrolytic experiments seemed to show clearly that all the hydrogen 
particles bore the same charge. They should, therefore, repel each 
other, and there appeared to be no basis for Avogadro's postulation of 
hydrogen molecules formed from two or more hydrogen atoms. Sim- 
ilarly, all the oxygen atoms appeared to be alike in bearing some other 
characteristic charge, so that they too should repel each other rather 
than aggregating in stable polyatomic molecules. Consequently, Avo- 
gadro's speculations, founded on the supposition that such polyatomic 
molecules had a real existence, appeared to be excessively farfetched 
when viewed in the light of a dualistic conception that arose quite 
straightforwardly from well-established observations of the chemical 
effects of electricity. Thus the dualistic theory struck a telling blow 
at the very foundation of the conceptual structure reared by Avogadro. 

Berzelius Conception and his Efforts to Secure Accurate Atomic 
Weights. Unlike Dalton, Berzelius accepted as exact Gay-Lussac's law 
of combining volumes. However, being unimpressed by Avogadro's 
attempt to reconcile the atomic theory with the law of combining vol- 
umes, Berzelius devised an alternative method of reconciliation that 
appeared to be much more prepossessing. This method did not entail 
the postulation of the polyatomic molecules of the elements, so re- 
pugnant to the dualistic view of chemical combination. Berzelius 
avoided all necessity for any such postulation by adopting the "equal 
volumes-equal numbers" notion only in a severely restricted form. 
He granted that there were equal number of gaseous particles (here 
assumed to be atoms) in equal volumes of the elementary gases, but 
he denied the extension of this supposition to the particles of the 
compound gases formed by the combination of the elements. Instead, 
he believed that the numbers of particles (molecules) in equal volumes 
of compound gases were not equal, but varied with the effective sizes 
of the molecules. In general he assumed, quite plausibly, that a mole- 
cule containing two or more atoms must have a greater effective 
volume than the individual atoms themselves, so that there ought to 
be fewer molecules in a volume of a compound gas than there were 


atoms in an equal volume of one of the component elementary gases, 
He allowed the molecular sizes to assume any values that brought 
the "predicted" numbers of molecules into line with the volume re- 
lations observed by Gay-Lussac. Let us consider a few examples of the 
results that are secured from this line of reasoning. 

For the combination of nitrogen and oxygen to form nitrous gas 
Avogadro would have written, as we do today, 

i volume oxygen + i volume nitrogen - 2 volumes nitrous gas, 
n particles + n particles - 2n particles, 

O 2 + N 2 - 2 NO. 

He suggests, in his text (see page 287), that it would be very difficult 
to construe the reaction in any other terms. But Berzelius found no 
difficulty in so doing, He would write 

i volume oxygen + i volume nitrogen - 2 volumes nitrous gas, 
n particles + n particles - n particles, 

O + N -* NO. 

Berzelius thus acknowledged that there were equal numbers of the 
respective atoms in equal volumes of nitrogen and oxygen. However, 
he regarded the molecules of nitrous gas as correspondingly bigger 
than the atoms constituting them. Indeed, in this case the volume of 
the molecule appeared to be just equal to the sum of the volumes of 
its component atoms a most attractively reasonable relation. There 
would then be only half as many molecules in a given volume of 
nitrous gas as there were atoms in an equal volume of nitrogen or 
oxygen. Consequently, if there were n atoms in one volume of oxygen 
or nitrogen, there would be but n molecules in two volumes of nitrous 
gas. The "predictions" of the atomic theory can thus be brought into 
line with the volume relations observed by Gay-Lussac, and this con- 
cordance involves neither the subdivision of the chemical atom nor 
the assumption of polyatomic molecules of the elements. 
Reasoning in the same way, Berzelius would have written 

i volume oxygen + 2 volumes hydrogen - 2 volumes water, 
n particles + 2n particles - n particles, 

O + 2 H - H 2 O 


i volume nitrogen + 3 volumes hydrogen - 2 volumes ammonia, 
n particles + yi particles - n particles, 
N + sH -> NH 3 . 

In each case the effective volumes of the product molecules were taken 
to be just those that would permit the number of available molecules 

300 CASE 4 

to fill the experimentally determined volumes of product. Thus Ber- 
zelius proposed to retain both the atomic theory and the law of com- 
bining volumes, He viewed the latter as highly significant as far as 
the numbers of atoms of the elementary gases were concerned, but he 
regarded the volumes of the product gases as more or less accidental 
factors which shed no great light on the numbers of compound mole- 
cules present. 

It seems probable that, had he not been diverted by his interpreta- 
tion of the physical phenomena through which he first made his 
oblique approach to the atomic theory, Dalton might have arrived at 
the well-formulated views adopted by Berzelius. These physical con- 
siderations (see page 226) so strongly suggested to Dalton that the 
effective diameters of no two gaseous species could be exactly the 
same that he was never able to credit the idea that equal volumes of 
different gases contained precisely the same number of particles. Con- 
sequently, he could never bring himself to accept the law of combining 
volumes as an exact relation, as Berzelius did. Thus, although he was 
the originator of the modern atomic theory, Dalton was outstripped 
by Berzelius in the appreciation of the significance and usefulness of 
the relations discovered by Gay-Lussac. Indeed, it might be even more 
correct to say that because Dalton was the originator of the modern 
atomic theory, and because of the way in which he received his original 
inspiration from the study of physical phenomena, he was less able 
to contribute to the subsequent elaboration of the chemical atomic 

It will be observed that this mode of approach gave Berzelius the 
"correct" formulas for water, ammonia, nitrous gas and a number of 
other compounds formed from gaseous elements. Unfortunately, only 
four of the then known elements are gases under normal conditions 
of temperature and pressure, so that the usefulness of this method of 
establishing molecular formulas was severely restricted. In the attempt 
to determine the atomic weights of the nongaseous elements Berzelius 
was thus forced to set out with a body of working rules reminiscent 
of Dalton's rule of greatest simplicity. Berzelius' rules were a great 
deal more sophisticated, and he applied them with flexibility and 
wisdom, guiding himself with a variety of crosschecks based on the 
analogies in the chemical behavior of the various elements and com- 
pounds. Even so, the atomic weights that he so deduced were often 
in error. However, they differed from Dalton's in one pivotally im- 
portant respect in practically all cases they diverged from the "cor- 
rect" (i.e., modern) values only by some small whole-number factor. 

This crucial difference obtained because the combining weights on 
which Berzelius' atomic weights were based were vastly more accurate 


than those used by Dalton. Berzelius secured these combining weights 
by the most laborious experimentation. He set himself to this immense 
task because he recognized it as a vital preliminary to the further 
progress of the atomic theory that had so favorably impressed him 
(see page 275). As he later wrote: 

By new experiments I soon convinced myself that Dalton 's figures were 
wanting in that accuracy that was required for the practical application 
of his theory. I perceived that if the light that was now shed upon the 
whole of science was to be increased, the atomic weights of as large a 
number of elements as possible, and especially those of the commonly 
occurring elements, must be determined with the greatest accuracy 

Perceiving that these accurate atomic weights would have to be based 
on accurate evaluations of the combining weights, Berzelius devoted 
the greater part of 10 years of his life to the careful determination of 
some 2000 combining weights of elements and compounds. These re- 
sults he collected and published in 1818. 

Let us contrast the state of affairs before and after Berzelius' work. 
Prior to his excellent determinations of combining weights there was 
a wide range of values for each atomic weight. For example, the 
weights of hydrogen and oxygen that combined to form water were 
so uncertain that the atomic weight of oxygen relative to that of 
hydrogen was very seriously in doubt, as may be seen from Table 2. 

TABLE 2. Atomic weight of oxygen (relative to hydrogen as i) according to 
various combining weights and formulas for water. 

// the combining Then the assumption of the following formulas leads 
proportions arc to the atomic weights shown 


H 2 



Dalton 1806 





Dalton 1810 





Avogadro 1811 




There is obviously a great diversity of possibilities and, although the 
conjectures based on any one set of combining weights are simply 
related to one another, those drawn from different evaluations of the 
combining weights are not. 

After Berzelius' work became available the situation was quite dif- 
ferent. The possible values of the atomic weights were strictly de- 
limited and very simply related to one another even when, as in his 
work with solid elements, Berzelius did not have Gay-Lussac's data 
to guide him. The restricted degree of uncertainty attaching to the 

302 CASE 4 

atomic weight of silver (symbol, Ag) will serve to illustrate the new 
state of affairs. It should be remarked here that Berzelius, unlike 
Dalton and Avogadro, referred all of his atomic weights to the weight 
of the oxygen, not the hydrogen, atom. Allowing the oxygen atom its 
present standard weight of 16, Berzelius' considerations might be 
formulated as follows: 

The fact is that 13.516 grams of silver combine with i gram of 
oxygen. Therefore, if the formula of silver oxide is AgO, 

atomic weight of silver _ atomic weight of silver _ 13.516 
atomic weight of oxygen 16 i 


atomic weight of silver = 16 X 13.516 = 216.26; 

if the formula of silver oxide is Ag 2 O, 

2 X atomic weight of silver 2 X atomic weight of silver _ 13*516 

atomic weight of oxygen 16 i 


atomic weight of silver = 8 X 13.516 = 108.13; 

if the formula of silver oxide is AgO 2 , 

atomic weight of silver atomic weight of silver 13.516 

2 X atomic weight of oxygen 2X16 i 


atomic weight of silver = 32 X 13.516 = 432.52; 

if the formula of silver oxide is A.g v O q9 where p and q represent any 
small integers, 

f X atomic weight of silver p X atomic weight of silver 13*516 

q X atomic weight of oxygen q X 16 i 


q q 

the atomic weight of silver = 16 X 13.516 = 216.26 . 

f P 

These possibilities are summarized in Table 3, which is similar to 
Table 2. However, it is immediately apparent that the range of possible 
atomic weights is much more restricted in Table 3. 

Making the best possible use of his very tenuous criteria for the 
selection of the correct formula, Berzelius tentatively adopted the for- 
mula AgO 2 , and the corresponding atomic weight of 432.52. In this 
choice he was mistaken, and it might appear that the range of possibil- 
ities was still so great that little positive progress had been made. How- 


ever, Berzellus* careful experimental work had at last removed serious 
doubts about the accuracy of the primary data, and the residual uncer- 
tainties all arose in the interpretation applied to them. Thus, in the 
present case, it was at least possible to say that if the atomic weight of 
silver were not 432.52, then it must be some simple multiple or fraction 
of that figure. Even this broad definition of the possibilities was such a 
notable advance over the previous uncertainties that It was rapidly 
fruitful of new advances. 

TABLE 3. Atomic weight of silver (relative to oxygen as 16) according to 
various formulas for silver oxide. 

The combining ratio of silver The possible values for the atomic weight of silver, 

to oxygen in silver oxide deduced from the following formulas, arc 











Petit and Dulong Lin\ the Atomic Theory to the Theory of Heat. 
Perhaps the most significant development arising from Berzelius' 1818 
publication was the work of two French investigators, Petit and 
Dulong, who announced the discovery of a most significant empirical 
generalization in a paper presented to the French Academy of Science 
on April 12, 1819. We have seen Berzelius' important dualistic theory 
growing out of the new interest in the recently discovered electrochemi- 
cal phenomena; the next episode in our story occurred because of a con- 
tinuing scientific interest in thermal phenomena, Dalton's response to 
which had already played a prominent role in shaping his atomic 
theory (see, for example, pages 224-226). 

It has not been our intent to provide extensive documentation for 
this epilogic summary. However, Petit and Dulong's account of their 
discovery of a generalization that related thermal phenomena to the 
atomic theory, is at once so clear and so revealing that we can scarcely 
forego its consideration. 

Investigations of Several Important Aspects of the Theory of Heat 
Considerations grounded on the totality of the laws relating to the 
properties of chemical compounds now allow us to form ideas about the 
constitution of bodies that, although they are arbitrarily established at 
several points, cannot be regarded as vague and absolutely sterile specu- 
lations. We are persuaded that certain of the properties of matter would 
appear in simpler form, and could be expressed in more regular and less 
complicated laws, if one could relate them to the elements on which they 
are immediately dependent. We have tried to introduce the most probable 

304 CASE 4 

results of the atomic theory [presumably Berzelius' figures] in the study 
of several of these properties that seem to be more intimately connected 
with the individual action of the particles of matter. The success that we 
have already attained makes us hope that this kind of reasoning will not 
only contribute to the ultimate progress of physics, but that also the 
atomic theory will in its turn receive from it a new degree of probability, 
and that it will there find sure criteria for the distinction of the truth 
among hypotheses that appear to be equally probable [i.e., for the selec- 
tion of the correct formulas and atomic weights]. 

Petit and Dulong now focus attention on the thermal properties, 
notably the specific heats, of various kinds of matter, to the study of 
which they had already made considerable contributions. The specific 
heat of a substance is here defined as the ratio between the quantity of 
heat required to produce a unit temperature change in a certain weight 
of the substance, and the quantity of heat required to produce the same 
temperature change in the same weight of water. Thus, a statement 
that the specific heat of some substance is o.i signifies that, for example, 
the quantity of heat required to warm one pound of this substance by 
iF would be only one-tenth as great as that required to warm one 
pound of water by iF. Petit and Dulong point out the inadequacies 
of the then current theories dealing with the specific heats of bodies, 
and further suggest that the available methods for the experimental 
determination of specific heats also leave much to be desired. After 
describing an improved method that they had devised for these measure- 
ments, they continue: 

We now present, in a single table, the specific heats of several elements, 
restricting ourselves however to those determinations about which we no 
longer entertain doubt [Table 4] . 

To bring out the law that we propose to make known we have, in the 
preceding table, joined to the specific heats of the different elements the 
relative weights of their atoms. As is known, these weights are deduced 
from the relations that one observes between the weights of the elements 
that combine with each other. The care that has been exercised for several 
years in the determination of the [weight] proportions in the majority 
of chemical compounds cannot leave more than slight uncertainties in 
the results of which we have made use. However, since there exists no 
rigorous method for the discovery of the real number of atoms of each 
species that enters into the compound [that is, there is no method of 
establishing the formula of the compound], one understands that there 
is always some arbitrariness in the establishment of the relative weights 
of the elementary molecules [atoms]. Nevertheless, the indeterminacy 
that so results does not extend to more than two or three numbers that 
are very simply related to one another [see page 302]. The reasons that 
have guided us in our choice will be sufficiently explained by what 


follows. [Petit and Dulong simply chose the simplest fractions of 
Berzelius' figures that yielded results in accord with the generalization 
they sought.] For the moment we will say only that there is no figure 
on which we have settled that is not in accord with the best established 
chemical analogies. 

The type of cross check implied by this statement is particularly clear 
and significant in the case of sulfur. The analogies between the chemi- 
cal behavior of sulfur and oxygen both as free elements and in their 

TABLE 4. Petit and Dulong's table of specific heats, atomic weights (con- 
verted to O = 1 6), and the products of these two numbers. 


Specific heat 
(relative to 

Products of the 
weight of each atom 
multiplied by the 
Relative weights corresponding 
of the atoms specific heat 

Petit and Dulong's 
"relative weights of 
the atoms" as derived 
from Berzclius' 1818 
figures * 





283.8 x y* 





414-2 x y* 





397-8 X 1 A 





178-4 X i 





253-3 x % 





432-5 X YA. 





129.0 X */t 





129.0 x y* 





I26.62X y* 





118.3 X & 





io8. 5 5X # 





118.3 X */3 





32-ipX i 

* This column does not appear in the table given by Petit and Dulong. It has been 
added to exhibit their (unacknowledged) indebtedness to Berzelius. The figures to the 
left in this column represent Berzelius' atomic weights which, when they are multiplied 
by the simple fractions on the right of the column, yield products that are in all cases close 
to, if not identical with, Petit and Dulong's relative atomic weights, as they are given in 
the third column of the table. 

compounds with other elements are striking. The prevalence of 
these similarities led quite naturally to the supposition that the com- 
pounds of sulfur and oxygen were analogous in general, and that they 
had analogous formulas in particular. Now in the case of water, 
Berzelius' use of Gay-Lussac's combining volume data led to the 
modern formula, H 2 O. It was then not unnatural to accept for 
the formula of the corresponding compound of sulfur with hydrogen 
the expression H 2 S. The use of this formula and the corresponding 
combining weights then leads to an atomic weight for sulfur of 32. 
This agrees well with the indication of the Petit and Dulong "law," 

306 CASE 4 

and presumably this "law" was originally framed with some attention 
to the inferences drawn from just such analogies. 

By means of the data contained in the preceding table it is now pos- 
sible to make a simple calculation of the relations that exist between the 
[heat] capacities of the different kinds of atoms. Observe, in this con- 
nection, that to pass from the experimentally observed specific heats to 
the specific heats of the particles themselves, it will suffice to divide the 
former by the numbers of particles contained in equal weights of the 
substances to be compared. Now it is clear that in equal weights of 
matter the numbers of particles are inversely proportional to the densities 
[weights] of the atoms. Thus the desired results will be secured by 
multiplying each of the experimentally determined specific heats by the 
weight of the corresponding atom. These products are gathered together 
in the fourth column of the table. 

This reasoning is only superficially complicated. The measured 
specific heats refer to the relative quantities of heat required by equal 
weights of the different substances. What Petit and Dulong sought were 
the quantities of heat required by equal numbers of atoms of the differ- 
ent substances. They remark that the heavier the atoms of an element, 
the smaller will be the number of its atoms contained in a certain 
weight of the element. Thus, for example, if the atoms of element A 
are ten times as heavy as those of element B, it is plain that in equal 
weights of A and B there will be only one-tenth as many atoms of A 
as of B. Equal numbers of atoms of the two species would be present 
only if we had ten times as great a weight of A as of B. In general, then, 
to study equal numbers of atoms of the different elements we must 
consider weights of these elements that are directly proportional to the 
relative weights of their atoms that is, to their so-called atomic 
weights. Consequently, to convert the heat requirements of equal 
weights of the different elements (i.e., the specific heats) to the heat 
requirements of equal numbers of atoms of the different elements, we 
have only to multiply the specific heats by the atomic weights. This is 
what Petit and Dulong did in arriving at the figures given in the fourth 
column of their table. 

Mere inspection of these numbers reveals a relation so remarkable in 
its simplicity that in it one immediately recognizes the existence of a 
physical law capable of being generalized and extended to all the ele- 
ments. In fact, the products in question, which express the [heat] 
capacities of different kinds of atoms, are so nearly equal to each other 
that it is impossible that the very slight observed differences are not 
attributable to the inevitable errors, whether these errors be in the meas- 
urement of the specific heats or in the chemical analyses. [This was an 
overly optimistic appraisal. The "law" is, in fact, far from exact.] This 


Is especially probable when It is observed that in certain cases the errors 
arising from these two sources may be in the same direction, so that they 
may be multiplied in the results. The number and diversity of the 
substances with which we have worked exclude the possibility of con- 
sidering as simply fortuitous the relation that we have just indicated, 
and justify the deduction of the following law: 

The atoms of all the elements have exactly the same capacity for heat. 

Recalling what we have said previously about the type of uncertainty 
that still attaches to the determination of the relative weights of atoms, 
It is easily seen that the law that we have just established might be 
changed if one were to adopt an assumption about the weights of the 
atoms that is different from the one we have used. In all cases, however, 
that law will embody the expression of a simple relation between the 
weights and the specific heats of the elementary atoms. Having to choose 
between equally probable hypotheses, we have felt obliged to decide in 
favor of the one that established the simplest relation between the ele- 
ments that we compared. 

Whatever may be the final opinion adopted with regard to this relation, 
it can henceforth serve as a control of the results of chemical analysis. 
In certain cases it may even offer the most exact method of arriving at 
information about the proportions of certain combinations. And if, in 
the continuation of our work, no fact arises to Impair the probability of 
the opinion that we now hold, this law will also offer the advantage of 
establishing in a certain and uniform manner, the relative weights of the 
atoms of all the elements that can be subjected to direct examination. 

Petit and Dulong now go on to consider the degree to which the 
data of other investigators agree with their law, and conclude with an 
exposition of the importance of their work for the general theory of 
heat. For our purposes, however, their most important contribution is 
alluded to in the last paragraph above, where it is suggested that the 
new "law" provides an important method of determining molecular 
formulas and atomic weights. The great significance of this new pos- 
sibility will be better appreciated after a closer examination of the key 
relation that lay at the bottom of all the earlier work on the atomic 

The Interrelation of Atomic Weights, Molecular Formulas, and 
Combining Weights. The combining weights (or proportions) of the 
elements in chemical compounds are determinable by direct measure- 
ments with the analytic balance. These combining weights are so re- 
lated to two other items the atomic weights of the elements and the 
molecular formulas of their compounds that if any two of these three 
factors are known the third can be computed. We may visualize this 
relation in the form of an equilateral triangle: if the positions of any 
two of the apexes of the triangle are known, the third can be located. 

308 CASE 4 

Now of the three interrelated factors only one the combining 
weights could be measured directly. Yet before use could be made of 
this crucial relation one of the other two factors had to be determined. 
The combining weights having been established, the molecular formulas 
could be calculated if the atomic weights were known; or the atomic 
weights could be calculated if the molecular formulas were known. 
But neither the atomic weights nor the molecular formulas were 
known, nor could they be determined by direct experimentation. Under 
these conditions there appeared to be no alternative to a resort to guess- 
work, and Dalton, Avogadro, Berzelius, and their contemporaries were 
constrained to adopt such a course. In general, they sought to guess at 
the molecular formulas by the use of a discordant variety of arbitrary 
working rules, the observed combining volumes of gases, the analogies 
between the chemical behaviors of the different elements, and so on. 
With these formulas and the known combining weights they then 
calculated the corresponding atomic weights. However, although the 
few formulas that could be deduced from the combining volumes of 
gases were largely correct, the greater number of molecular formulas 
were very poorly established, and largely rested on extremely conjectural 
foundations. There thus remained the gravest doubt about the validity 
of the calculated atomic weights, as may be seen from an examination 
of the various possible values for the atomic weight of silver given on 
page 302. 

Petit and Dulong's new generalization sharply reduced the conjec- 
tural element in the appraisal of atomic weights. Even though their 
"law" was neither as general as they had hoped nor as accurate as 
they had supposed (its fallibility was very properly recognized by 
Berzelius at an early date), this '"law" did at least provide approxi- 
mate values of the atomic weights. Curiously enough, the availability 
of these quite crude values made possible a fruitful return to the 
"triangular" relation, and through it led to the derivation of accurate 
atomic weights that were more firmly rooted against the winds of 

This new possibility is well illustrated in the case of silver. Reference 
to page 302 shows that the combining weights of the elements in silver 
oxide were well established. However, in the absence of sure criteria 
for the selection of the proper molecular formula, there was a series of 
possible values for the atomic weight of silver. Now let us take advan- 
tage of Petit and Dulong's "law" that the product of the atomic 
weight and the specific heat is approximately constant. The average 
value of this "constant," deduced from their figures, was 6.0. For the 
specific heat of silver they cite the figure 0.0557. According to their 
"law," then, it should be true that 


Atomic weight of silver X specific heat of silver *** 6.0; 
Atomic weight of silver X 0.0557 =*= 6.0; 

Atomic weight of silver - = 107.7. 


This is not the exact value that Petit and Dulong had supposed it would 
be both because of the serious experimental difficulties besetting the 
accurate determination of specific heats, and because of their "law's" 
inherent failings. But this approximate value is all we need! 

Looking back to page 303 we see that of the various possible formulas 
for silver oxide only one, Ag 2 O, leads to the deduction of an atomic 
weight of silver that is anywhere in the vicinity of the approximate 
value. Thus it appears that we are justified in settling on Ag 2 O, rather 
than Berzelius' choice of AgO 2 , as the most probable formula of silver 
oxide. Now we have both the combining weights and the molecular 
formula, so that we can solve for the third factor the atomic weight 
of silver by the routine method shown on page 302. It is plain that the 
approximate value of the atomic weight has played the limited but 
crucial role of providing a more reliable criterion for the selection of 
the proper molecular formula; and once this was established, the calcu- 
lation of the atomic weight could be carried out by the standard meth- 
ods used by Dalton, Berzelius, and others. 

Petit and Dulong's "law" thus opened up an important avenue of 
approach to the determination of atomic weights and molecular for- 
mulas. It provided a vital complement to the suggestions furnished by 
the data on gas densities and combining volumes which, as they were 
used by Berzelius, could be applied only to the relatively few elements 
that were normally gaseous. The atomic weights of the vast majority of 
elements had previously been deduced with the aid of various arbitrary 
working rules, but these rules could now be discarded in favor of the 
more objective indications drawn from the "law" of Petit and Dulong. 
To the methods founded on this "law" and on the data on gas den- 
sities and combining volumes Berzelius joined two others, one based 
on the analogies in the chemical behavior of the elements (see page 
305), the other based on analogies in the crystal structure of com- 
pounds. By judicious selections from among the various possibilities 
offered by these methods he had, by 1840, arrived at atomic weights 
and molecular formulas that are in most cases in excellent agreement 
with those we now accept as correct. But alas, by this time a flood 
tide of skepticism was already lapping around the foundations of the 
atomic theory, and Berzelius' fine work did not receive the attention it 

Perplexing Results of Dumas' Vapor-Density Studies (1827). Many 

310 CASE 4 

factors contributed to the outburst of a long-latent skepticism about the 
"reality" of the whole structure of matter postulated by the atomic 
theory. One in particular is worthy of our closer attention. Avogadro 
had suggested that the relative weights of the particles of the gaseous 
elements could be inferred from the corresponding relative gas densi- 
ties. Until 1826 this method had had a very limited application, since 
only four of the then known elements were gaseous under normal con- 
ditions of temperature and pressure, The Petit and Dulong "law" could 
not be efficiently applied to these gaseous elements and, consequently, 
there had been no satisfactory check on the consistency of the atomic 
weights derived from the Petit and Dulong "law" and those secured 
from gas-density data. But in 1827 enough data became available to 
permit a limited comparison of the atomic weights indicated by these 
two methods. The results then obtained, far from showing the eagerly 
anticipated concordance, manifested an apparent incompatability that 
shook the atomic theory to its very roots. The involuntary engineer of 
this deplorable denouement was the French chemist J. B. A. Dumas, 
then at the threshold of a brilliant career. 

Dumas began by being very favorably impressed by the possibilities 
of the gas-density method, and he proposed to extend its usefulness. 
For this purpose he devised a simple yet elegant procedure (which is 
still used today) for the determination of gas densities at such high 
temperatures that a considerably increased number of elements could 
be studied in the gaseous state. This method he applied to a variety of 
substances. Let us consider the surprising results he obtained for the 
elements mercury, sulfur, phosphorous, and arsenic. 

The density of mercury vapor was found to be just about 100 times 
that of hydrogen at the same temperature and pressure. The application 
of the "equal volumes-equal numbers" idea to this datum leads to the 
conclusion that the particles of mercury are 100 times as heavy as those 
of hydrogen. But the Petit and Dulong "law" and the combining- 
weight data indicate an atomic weight of mercury in the vicinity of 200. 

To Berzelius the "particles" in a gaseous element were atoms, (It 
will be recalled that his dualistic theory had induced him to neglect 
the possibility of polyatomic molecules of the elements.) Therefore the 
gas-density data would indicate that the mercury atom was 100 times 
as heavy as the hydrogen atom, a serious contradiction of the value of 
200 obtained from the other sources. This discrepancy, together with 
others discussed below, impelled Berzelius to break off the struggle. 
He simply concluded that the "equal volumes-equal numbers" idea 
applied only to the elements that were gaseous at room temperature, 
and he denied the validity of its application to the less volatile elements 
studied by Dumas. Such an artificial distinction was repugnant to 


Berzelius' contemporaries, as it probably was to him, but he saw no 
more palatable alternative. 

Dumas was more willing than Berzelius to consider the possibility 
o polyatomic molecules of the elements, but whether one says that the 
gaseous particles of mercury (symbol, Hg) and hydrogen are Hg and 
H, or Hg 2 and H 2 , or Hg 4 and H 4 , or Hg w and H n , it is plain that if 
there are equal numbers of these particles in equal volumes of the 
respective elements, there must also be equal numbers of the corres- 
ponding atoms. Thus the problem is still unresolved the total weight 
of a number of atoms of mercury is only 100 times the weight of an 
equal number of atoms of hydrogen. The indicated atomic weight of 
mercury is then 100, only half that suggested by the Petit and Dulong 

A discrepancy of the same sort, but in the opposite direction, arose in 
the case of sulfur. The Petit and Dulong "law" indicated that the 
atomic weight of sulfur was 32, which agreed with the value obtained 
from the combining weights when the formulas of sulfur compounds 
were so assigned as to bring out the chemical analogies between sulfur 
and oxygen. But the measured density of sulfur vapor was 96 times that 
of hydrogen. Acceptance of the "equal volumes-equal numbers" notion 
then implied that the sulfur particles were 96 times as heavy as those 
of hydrogen. Whether to these particles one assigned the formulas 
S and H, or S 2 and H 2 , or S w and H n , it was all too clear that if the 
numbers of these particles were equal, the numbers of the correspond- 
ing atoms would also be equal. Hence the atomic weight of sulfur was 
indicated as 96, three times the then accepted value derived from 
other sources. The vapor-density studies of phosphorus and arsenic led 
to similar contradictions, since these densities proved to be twice as 
great as had been expected. The cumulative inconsistency is impressive, 
and it is little wonder that Berzelius adopted the easy way out com- 
pletely rejecting the application of the "equal volumes-equal numbers" 
idea to these cases. 

There is, to be sure, one ingenious way in which all of these contra- 
dictions can be resolved without discarding Avogadro's attractive idea. 
This rationalization was proposed in 1833 by Gaudin, another French 
investigator; and, to some extent, it was apprehended by Dumas him- 
self. Let us suppose that there are equal numbers of particles in equal 
volumes of the vapors of the different elements; but let us now further 
assume that these particles do not in every case contain the same 
number of atoms. 

Turning to a concrete example, let us imagine that the "particles" of 
mercury and of hydrogen are Hg and H 2 > respectively. Now, if there 
are n particles in unit volume of each of these gases, we are actually 

312 CASE 4 

dealing with n atoms of mercury and zn atoms of hydrogen. If we 
assign to hydrogen and mercury the accepted relative atomic weights 
of i and 200, then the following proportion will prevail: 

Weight of mercury in unit volume of mercury vapor _ n X 200 
Weight of hydrogen in unit volume of hydrogen gas 2n X i 

But, since the density of a gas is synonomous with the weight of unit 
volume of that gas, we may also write: 

Density of mercury vapor n X 200 

Density of hydrogen gas in X i 

= ioo ? 

and the predicted ratio of the densities of mercury and hydrogen is then 
precisely that found in practice. 

We may, in similar fashion, assign to the sulfur "particle" the formula 
S 6 . Then, if the number n of these particles in unit volume of sulfur 
vapor is the same as the number of H 2 particles in unit volume of 
hydrogen gas, we will have present 6n atoms of sulfur as against 2n 
atoms of hydrogen. If, now, we assign to the atomic weight of sulfur 
its most probable value of 32, we come to the following proportion : 

Density of sulfur vapor 6n X 32 
Density of hydrogen gas 2n X i 

and the predicted ratio of the gaseous densities is then in full agreement 
with that found by the direct measurements. The extension of this type 
of reasoning to phosphorus and arsenic reveals that if the "particles" of 
these substances are polyatomic molecules with formulas P 4 and As 4 , 
respectively, then there is again complete consistency between the 
atomic weights derived from the Petit and Dulong "law" and the com- 
bining-weight data on the one hand, and the relative gas densities and 
Avogadro's hypothesis on the other. 

This apparently attractive reconciliation could be achieved only at a 
price that many found inordinately high. Not only would it have to be 
maintained that there are polyatomic molecules of the elements, but it 
would now have to be further conceded that the polyatomic molecules 
of the different elements contain different numbers of the respective 
atoms. The source of the stability of any polyatomic molecule was un- 
known the whole conception was repugnant to the influential dual- 
istic theory and to this difficulty would now be added the inability 
to explain why the molecules of different elements contain different 
numbers of their respective atoms. It would be necessary to hypothesize 
not just one improbable, but a considerable variety of improbables; and 
the diversity of these formulas for the incongruous polyatomic molecules 


seemed a flagrant violation of the scientist's almost instinctive faith in 
the simplicity of nature. 

An equally serious shortcoming was that, if the variation of the 
number of atoms per molecule of the gaseous elements were accepted, 
the usefulness of Avogadro's original proposal appears to be very 
seriously impaired. The postulated equality of the number of "particles" 
present in equal volumes of the different gaseous elements could not 
now be assumed to signify the equality of the number of atoms of these 
elements, so that measurements of the relative gas densities of the 
elements could no longer be construed as the basis of a distinct evalua- 
tion of the relative atomic weights. For such an evaluation it would be 
necessary to know the relative numbers of atoms present, and this in 
turn depended on a knowledge of the numbers of atoms present in the 
gaseous "particle" of each element. It will be recalled that one of the 
major weaknesses of Avogadro's original proposal was his inability to 
suggest any method of estimating the numbers of atoms in the mole- 
cules of the gaseous elements, and this deficiency now assumed major 
significance. One could infer these numbers if atomic weights drawn 
from other sources were used in the interpretation of the measured 
gas densities. However, the very fact that these other atomic-weight 
data were required suggested that gas-density values could not provide 
the basis for a significant independent method of determining atomic 
weights. One might adopt Berzelius' view, denying that the "equal 
volumes-equal numbers" notion applied to elementary gases except in 
special cases. Or one might, apparently, vitiate the significance of this 
notion by adopting the further conjecture that the "particles" involved 
contained different numbers of atoms. But in either case the conclusions 
appeared to involve the destruction of much of the value of Avogadro's 

Confusion and Dawning Clarification of the Atomic Theory in the 
Period 1827-1857. Hastening toward our conclusion, let us once again 
examine three important weak points in Avogadro's scheme, with a 
consideration of which this epilogue began. These points provide some 
basis for a very rapid survey of the events that most affected the atomic 
theory during the period between the setback it experienced through 
Dumas' work in 1827 and its triumphant revival by Cannizzaro in 

The first of these points was the conjectural character of the atomic 
theory in general, and of Avogadro's proposals in particular. This un- 
avoidable characteristic caused a certain amount of skepticism in the 
earliest days of the atomic theory, and the doubts waxed stronger after 
Dumas' vapor-density work. Skepticism probably reached its peak a 
little after 1840, about the time of the accelerated decline of Berzelius' 

314 CASE 4 

duallstic theory. Even as the bankruptcy of a major concern shakes the 
whole of the business world, the decline of Berzeiius' towering concep- 
tual scheme, brought about by some other experimental work of 
Dumas', inferentially involved in its ruin the atomic theory, of which 
Berzelius had been one of the foremost proponents. 

The atomic theory was far from dead, but for a time it appeared 
quite infirm. Yet scarcely one of the years between 1827 and 1858 passed 
without the development of some more or less compelling evidence of 
the "correctness" of the corpuscular view of matter. A host of newly 
discovered properties and phenomena relating to the manifold com- 
pounds of carbon were very successfully construed in terms of the 
atomic theory. In particular, there were certain striking regularities in 
the vapor densities of the many gaseous compounds of carbon; and, in 
the years between 1843 and 1856, Gerhardt and Laurent repeatedly em- 
phasized how easily these regularities could be understood in terms of 
simple relations based on the "equal volumes-equal numbers" idea. 
The originally limited scope of application of Avogadro's proposal was 
thus vastly extended, and the value and significance of this proposal 
were correspondingly increased. Then, too, by 1857 an impressive success 
was finally achieved in the long search for a method of deducing or 
deriving the properties of gases from the laws of mechanics. Among 
other things, the new "kinetic theory of gases" strongly indicated that 
gases consisted of minute particles of matter, widely separated from 
each other and present in equal numbers in equal volumes of elemen- 
tary and compound gases. Perhaps even more striking was the intima- 
tion that some of these particles were polyatomic molecules of the ele- 
ments, just as postulated by Avogadro. 

Still another factor, less immediate in its action though probably of 
great importance, was the scientific world's increasing awareness of the 
profound fruitfulness and frequent "correctness" of a wide variety of 
other speculative schemes. By 1857 these new sentiments may have 
reduced the antipathy toward the conjectural character of the Dalton- 
Avogadro conceptual scheme, particularly since the plausibility of this 
scheme had been much increased by all the developments noted above, 
and many others as well. Though its conjectural character was still a 
distinct liability, it was probably no longer a major source of resistance 
to the free acceptance of this surpassingly useful conceptual scheme. 

A second weak point to which attention has been directed was the 
lack of any adequate explanation of the stability of the polyatomic mole- 
cules of the elements postulated by Avogadro. With the decline and 
fall of Berzelius* dualistic theory the antipathy to such bodies was 
somewhat reduced; at least their postulation was no longer a flat con- 
tradiction of an influential contemporary theory. Moreover, there were 


a number of independent indications that such polyatomic molecules 
did "exist." We have already commented on the important inference 
drawn from the kinetic theory of gases, and the existence of such bodies 
was also suggested by the observed variety of the physical forms of some 
of the elements, by the heats and speeds of various chemical reactions, 
and by a number of other phenomena with which we need not now 
concern ourselves. Thus, although by 1857 there had been practically no 
positive progress toward a satisfactory explanation of the existence of 
these polyatomic molecules, there was at least an accumulation of bits 
of evidence that they "did exist'' Presumably the postulation of these 
particles was still not an entirely palatable proposal, but it was probably 
no longer a major item of reproach against the Dalton-Avogadro 
conceptual scheme. 

We have also considered a third weak point the lack of a well- 
defined method of determining the numbers of atoms in the hypo- 
thetical molecules of the elements. By 1857 this had become a particu- 
larly vexing shortcoming, in that it deprived Avogadro's proposals of 
much of their intrinsic usefulness as the basis for an independent evalu- 
ation of the atomic weights of the elements. After Dumas' work the 
measured values of the relative gaseous densities of the elements could 
no longer be regarded as a direct and certain indication of the relative 
atomic weights of those elements. In the preceding paragraphs we have 
seen how two other major sources of difficulty in Avogadro's conceptual 
scheme had, by 1857, become somewhat less pressing. However, this 
third weakness, connected not with the abstract plausibility but with 
the concrete usefulness of Avogadro's scheme, had, if anything, become 
a more serious problem than before. Yet the need for a trustworthy 
series of atomic weights and molecular formulas had never been more 
acute. It was just this problem on which the Italian chemist Stanislao 
Cannizzaro (1826-1910) threw great light. In 1858 he both minimized 
its importance and indicated its solution, in connection with a most 
penetrating analysis of the Dalton-Avogadro conceptual scheme. 

The Final Act Cannizzaro Revives and Emphasizes Avogadro's 
Concept. It is from the appearance of Cannizzaro's Sketch of a Course 
of Chemical Philosophy that we can date the beginning of the final 
triumph of the atomic-molecular theory. Cannizzaro's deceptively 
simple proposal was founded on nothing more novel than a full return 
to Avogadro's original position. We are to assume that the numbers of 
particles in equal volumes of all elementary and compound gases are 
equal. We must not, however, confuse these particles (molecules) with 
the atoms of which they are composed. Neither must we so far give 
way to our longing to find simplicity in nature as to suppose that the 
molecules of all the gaseous elements contain equal numbers of their 

316 CASE 4 

respective atoms. This being granted, It is plain that we cannot expect 
to find equal numbers of atoms in equal volumes of the various elemen- 
tary gases. Consequently the direct comparison of the relative densities 
of the gaseous elements leads not to the relative atomic weights, but 
only to the relative molecular weights of those elements. However, 
while depreciating this superficially attractive possibility, Cannizzaro 
suggested a much more promising approach the comparison of the 
densities of the gaseous compounds of the elements. 

Let us begin with the case of hydrogen. We can measure the densities 
(i.e., the weights of unit volumes) of a wide variety of gaseous com- 
pounds of hydrogen. By analysis we can determine what proportion of 
the weight of each of these compounds is due to the hydrogen it con- 
tains. If, now, we multiply the measured density of each compound by 
the measured fraction of its weight that represents its hydrogen content, 
then we find the weights of hydrogen that are present in equal (unit) 
volumes of the gaseous compounds of this element. Very significantly, 
all these quantities prove to be integral multiples of one minimum 

How is this relation to be understood ? First we must remember that 
we are dealing with unit volumes of each of the different gases, hence 
with equal numbers of the respective molecules. Let us call this (un- 
known) number n. Let us now assume and this is still akin to a rule 
of simplicity that the molecule of at least one of these gaseous com- 
pounds of hydrogen contains just one hydrogen atom. The total weight 
of hydrogen present in unit volume of that compound should then be 
given by the expression n X weight of an atom of hydrogen. An equal 
weight of hydrogen will be found in the unit volume of any other gas 
whose molecule contains but one hydrogen atom. Moreover, this should 
be the minimum weight of hydrogen ever found under these condi- 
tions, since we cannot readily conceive of a hydrogen compound whose 
molecule contains less than one atom of hydrogen. Symbolizing this 
minimum weight of hydrogen by M H we may then write: 

M H = n X weight of an atom of hydrogen. 

Now if among the compounds studied we had one whose molecule 
contained two hydrogen atoms, then the weight of the hydrogen 
present in unit volume of this compound should be 2 X n X weight of 
an atom of hydrogen, or 2M#, Similarly, unit volume of a compound 
whose molecule contains three hydrogen atoms will contain a weight 
of hydrogen expressed by 3 X n X weight of an atom of hydrogen, or 
$M H , and so on. Therefore we have every reason to anticipate what we 
actually find: that all the weights of hydrogen are integral multiples of 
a certain minimum weight, which we have called M H . Incidentally, 


since the weight of unit volume of pure hydrogen is equal to 2M H) we 
have some justification for concluding that the gaseous "particle" of 
pure hydrogen is an H 2 molecule i.e., the molecule contains two 

Applying the same methods to the study of the gaseous compounds 
of oxygen, we find, as expected, that the weights of oxygen contained 
in unit volumes of these compounds are all integral multiples of some 
minimum value. This minimum weight of oxygen, which we shall 
designate as M 0? must represent the weight of oxygen present in n 
molecules of a compound that contains just one atom of oxygen in each 
of its molecules. Consequently we may write : 

M n X weight of an atom of oxygen. 

The experimentally determined value of M is just 16 times that of the 
analogous minimum weight of hydrogen, M H . Now we are in a position 
to make a very significant calculation. From the two foregoing equa- 
tions we may derive the following expression: 

n X weight of an atom of oxygen M 


n X weight of an atom of hydrogen M B 
weight of an atom of oxygen M 

weight of an atom of hydrogen M H 
But since experiment has shown that M = i6M H we may conclude that 

weight of an atom of oxygen M i6M H 16 
weight of an atom of hydrogen M H M H i 

whence it is plain that the atomic weight of oxygen, relative to the 
hydrogen atom taken as i, must be 16. Finally, since the weight of unit 
volume of pure oxygen is 2M , it appears that each molecule of gaseous 
oxygen must contain two oxygen atoms, and should be represented by 
the formula O 2 . 

Turning now to the element carbon, we encounter a material so very 
involatile (below 3000C its vapor pressure is exceedingly small) that 
direct measurement of its density in the gaseous state was essentially 
impossible. However, carbon forms a large number of volatile com- 
pounds, so that we can easily determine its atomic weight by the method 
proposed by Cannizzaro. An experimental study reveals that the 
weights of carbon present in unit volumes of its gaseous compounds are 
always integral multiples of a minimum value, which is 12 times the 
corresponding minimum figure for hydrogen. Hence the atomic weight 
of carbon is established as 12. 

318 CASE 4 

Applying the new method to the many gaseous compounds o sulfur, 
we secure the expected series of weights that represent integral multiples 
of a minimum weight of sulfur M g , and M s is 32 times the value of 
M Ht so that the indicated atomic weight of sulfur is 32. This is in ex- 
cellent agreement with the figure derived from the Petit and Dulong 
"law" and with the value deduced from the combining weights in 
sulfur compounds when the formulas of these compounds are assigned 
so as to bring out the chemical analogy between sulfur and oxygen. 
Incidentally, under the conditions prevailing in Dumas' vapor-density 
studies the weight of unit volume of pure sulfur vapor approximates 
6M S , suggesting S 6 as the formula of the sulfur molecule. 

The study of mercury by vapor-density methods alone is somewhat 
handicapped by the small number of readily volatile compounds of this 
element. When we have completed the examination of this limited 
series of compounds we cannot be too confident that we have at least 
one substance that contains but one atom of mercury in each of its 
molecules. For what it may be worth, however, M Sg , the minimum 
weight of mercury of which all the others are integral multiples, proves 
to be 20oMjy. The value of 200 so indicated for the atomic weight of 
mercury then agrees with that predicted by the Petit and Dulong 
"law." The weight of unit volume of pure mercury vapor is just equal 
to M Hff , so that for this element the gaseous "molecule" is identical with 
the chemical atom. 

Continuing this type of examination of the compounds of all the 
common elements, Cannizzaro emphasizes that in every case to which 
both the Petit and Dulong "law" and his own treatment of the vapor- 
density data can be applied, the two indications of the atomic weight 
are concordant. So general and impressive is this self-consistency that 
it seems almost impossible to avoid the conclusion that it represents the 
inevitable agreement of the results of two equally valid methods for 
the determination of atomic weights. As already remarked, these two 
methods display a favorable complementarity. The atomic weights of 
the light nonmetallic elements which form many volatile com- 
pounds are most readily deduced from gas-density measurements; 
and the atomic weights of the heavy metallic elements which do not 
form many volatile compounds are indicated by the Petit and Dulong 
"law." Thus, by the combined action of these two methods, we can at 
long last derive a rational and coherent series of the atomic weights of 
the elements. 

This development had many vital and widespread implications, but 
with its completion we may bring our present story to a close. We have 
seen how in 1808 Dalton called attention to "the importance and advan- 
tage of ascertaining the relative weights of the ultimate particles of both 



simple and compound bodies!" In 1858 Cannizzaro finally achieved the 
goal that had been indicated just half a century earlier. In the almost 
50 years that had elapsed since the first enunciation of the Dalton- 
Avogadro conceptual scheme practically nothing essential in that 
scheme had been changed. However, during the intervening period of 
intense scientific activitv there had been (i) a dissipation of some of 
the original objections to this scheme; (2) an accumulation of much 
indirect evidence in favor of it; (3) the collection of many data of 
critical importance to it; and (4) the development of an acute need for 
it. Its revival by Cannizzaro, in his supremely lucid, powerful, and 
convincing statement, rapidly swept this scheme to the prominent posi- 
tion among the concepts of science that it has continued to occupy with 
honor until the present day. 


1774-1789 Period of the "chemical revolution" brought about by the 

introduction of Lavoisier's oxygen theory of combustion 
1789 Wm. Higgins' proposal of an atomic theory 
1792-1802 Richter's work on the law of equivalent proportions 
1797-1808 Proust's work on law of definite proportions; challenged by 

Berthollet in 1801 

1800-1803 Dalton achieves a clear formulation of his atomic theory 
1803 Dalton's first public intimation of his atomic theory. State- 
ment to Thomson in the following year 

1807 First printed account of the atomic theory appears in 
Thomson's book 

1808 Publication of the first part of Dalton's New System of 
Chemical Philosophy 

1808 Thomson and Wollaston support the law of multiple pro- 

1809 Publication of Gay-Lussac's work on the law of combining 

1 8 10 Publication of second part of Dalton's New System, con- 
taining criticism of Gay-Lussac's work 

1811 Avogadro's publication the postulation of polyatomic 
molecules of the elements 

1811 Berzelius presents a brief account of his dualistic theory 
1818 Berzelius publishes a collection of a large number of com- 
bining and atomic weights 

320 CASE 4 

1819 Publication of Petit and Dulong "law" 
1827 Dumas' vapor density work 
1827-1857 Period of intense scientific activity and a rather confused 

response to the atomic theory 
1858 Publication of Cannizzaro's Sketch of a Course in Chemical 



Of the books that have been consulted in the preparation of this study the 
following have proved most generally informative. 

Alembic Club Reprints, No. 2, Foundations of the Atomic Theory, No. 4, 
Foundation of the Molecular Theory (E. and S. Livingstone, Teviot Place, 
Edinburgh, Scotland). 

John Dalton, New System of Chemical Philosophy, parts I and II (Man- 
chester, 1808-10). 

Ida Freund, The Study of Chemical Composition (Cambridge University 
Press, 1904). 

W. C. Henry, Life of Dalton (London, 1854). 

A. N. Meldrum, Avogadro and Dalton (Aberdeen University Studies, 
No. 10, 1904). 

J. R. Partington, A Short History of Chemistry (London, Macmillan, 1948). 

H. E. Roscoe and A. Harden, A New View of the Origin of Dalton' s 
Atomic Theory (London, Macmillan, 1896). 

A tabulation of the various quotations used in this study appears below. 
The page on which the quotation begins is listed in the first column; the 
author of the quotation in the second; and the source in the third. Brack- 
eted entries in the third column represent more accessible sources of texts 
the originals of which may not be readily available. 

222 Dalton Memoirs of the Literary and Philosophical Society of 

Manchester, Second Series, /, 271 (1805) [Alembic Club 
Reprint No. 2]. 

222 Dalton Roscoe and Harden, New View, p. 13. 

228 Dalton 

228 Dalton New System, pp. 142, 211. 

230 Dalton Ibid., p. 213. 

231 Thomson A System of Chemistry, ed. 3, vol. 3, p. 425 [Alembic 

Club Reprint No. 2]. 

234 Newton Roscoe and Harden, New View, p. 124. The quotation 
is from the Optics (ed. Horsley, 1782), vol. 4, pp. 260, 


224 Dalton Roscoe and Harden, New View, p. 71. 



238 Dalton 

238 Henry 

239 Proust 

240 Proust 

244 Wollaston 

245 Dalton 

247 Wollaston 

248 Berzelius 

250 Dalton 

251 Lavoisier 

253 Gay-Lussac 

258 Anon. 

264 Dalton 

265 Dalton 

266 Dalton 

267 Dalton 

268 Dalton 

272 Dalton 

273 Dalton 

274 Dalton 
274 Berzelius 
278 Avogadro 

280 Ampere 

294 Dalton 

296 Davy 

301 Berzelius 

303 Petit and 

So far as possible all the citations that are of major importance have been 
checked against the original publications; several that are o lesser signifi- 
cance have been drawn from secondary sources, as noted above. In some 
half-dozen instances individual words of the texts have been altered in the 
interest of clarity of expression. 

New System. 

Life of Dalton, p. 38. 

Freund, Study of Chemical Composition, pp. 137, 138. 

Ibid., p. 142. 

Phil Trans. 104, 5 (1814). 

Roscoe and Harden, New View, p. 117. 

Phil Trans. 98, 96 (1808); [Alembic Club Reprint 

No. 2]. 

Freund, Study of Chemical Composition, p. 162. 

New System, p. 275. 

Elements of Chemistry, Part r, Chap, i, trans, by Robert 

Kerr (1793 and many later editions). 

Memoir es de la Societe d'Arcueil 2, 207 (1809). The 

translation cited is that given in Alembic Club Reprint 

No. 4, 

Freund, Study of Chemical Composition, p. 304. 

Roscoe and Harden, New View, p. 27. 

New System, p. 71. 

Ibid., p. 189. 

Ibid., p.m. 

Ibid., p. 555. 

I bid., p. 316. 

Ibid^ p. 550. 

Roscoe and Harden, New View, p. 159. 

Ibid., p. 161. 

Journal de Physique 73, 58 (1811). The translation 

cited is based on, though different from, that given in 

Alembic Club Reprint No. 4. 

Freund, Study of Chemical Composition, p. 321. 

New System, p. 167. 

Phil 7V<ww,97,54(i8o7). 

Lehrbuch (1845). 

Ann. Chim. Phys. 10, 395 (1819). 



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